Subgroup Identification and Variable Selection from Randomized Clinical Trial Data
by
Jared C. Foster
A dissertation submitted in partial fulfillment of the requirements for the degree of Doctor of Philosophy (Biostatistics) in The University of Michigan 2013
Doctoral Committee: Professor Bin Nan, Co-chair Professor Jeremy M.G. Taylor, Co-chair Assistant Professor Lu Wang Professor Ji Zhu c Jared C. Foster 2013 All Rights Reserved For my wonderful family and beautiful fianc´e.
I couldn’t have done this without you.
ii ACKNOWLEDGMENTS
Thank you to Professors Jeremy Taylor, Bin Nan, Ji Zhu and Lu Wang, my dissertation committee, for all the very helpful questions and comments you have given me. Beyond this, I’d like to thank Jeremy and Bin, my co-advisors, for all the hours they spent meeting with me and all the useful advice they have given me. Bin, you introduced me to the incredibly fascinating field of variable selection, for which I am truly grateful. Jeremy, you introduced me to subgroup analysis and personalized medicine, which, combined with variable selection, has become my true passion. Additionally, despite my best efforts to become your most annoying student, you have been incredibly patient, thoughtfully responding to my many emails and discussing many ideas and issues with me whenever I randomly drop by your office.
You guys are awesome, and I am truly blessed to have had the opportunity to learn from both of you.
Thank you also to my office mates, past and present, for putting up with me and my love of conversation. Yong-Seok Park, Rebecca Andridge and Connie Lee were incredibly helpful when I was preparing for the qualifying exam. Anna Conlon,
John Rice, Jincheng Shen, Daniel Muenz and Oliver Lee, you have been very patient with me, and I have very much enjoyed our many fascinating conversations. Edward
Kennedy, Phil Boonstra and Laura Fernandes, thank you also for putting up with me, and for helping me to grow through our many philosophical and spiritual discussions.
iii To my parents, Dr. James and Mrs. Janet Foster, and Jenna and Jeff Spielmann, my sister and brother-in-law, thank you so much for all of your support throughout my life, especially these past seven years. You guys are amazing, and I love you all very much.
Finally, to the love of my life, Grace, thank you so much for all you have put up with these past seven years. You have been incredibly loving, patient and supportive, and have inspired me to become a better man. I definitely could not have done any of this without you. I can’t wait to spend the rest of my life with you!
iv TABLE OF CONTENTS
DEDICATION ...... ii
ACKNOWLEDGMENTS ...... iii
LIST OF FIGURES ...... vii
LIST OF TABLES ...... ix
CHAPTER
1. Introduction ...... 1
2. Variable selection in monotone single-index models via the adaptive LASSO ...... 7
2.1 Introduction ...... 7 2.2 Estimation for monotone single index models ...... 10 2.2.1 A smooth monotone function estimate for η with fixed β ...... 11 2.2.2 Estimation for β with fixed η ...... 13 2.2.3 Algorithm ...... 14 2.2.4 Asymptotics ...... 16 2.2.5 Bootstrap standard errors ...... 17 2.3 Simulations ...... 18 2.3.1 Examples ...... 19 2.4 Example data ...... 23 2.5 Discussion ...... 27
3. Selection of simple rules for treatment assignment using pa- tient information ...... 29
3.1 Introduction ...... 29 3.2 Identifying subgroups using the average value function . . . . 31
v 3.2.1 Nonparametric estimation of g and h ...... 32 3.2.2 Selecting a subgroup for fixed g and h ...... 33 3.2.3 Evaluation of the region Aˆ ...... 36 3.2.4 Selection of δ ...... 38 3.3 Simulations ...... 39 3.4 Application to randomized clinical trial data ...... 45 3.5 Discussion ...... 50
4. Permutation testing for treatment-covariate interactions .. 53
4.1 Introduction ...... 53 4.2 Permutation tests ...... 56 4.2.1 Review of permutation tests ...... 56 4.2.2 Modified permutation methods ...... 57 4.3 Simulations ...... 62 4.3.1 Simple linear model example ...... 63 4.3.2 Complex model example ...... 67 4.4 Application to data from a randomized clinical trial . . . . . 70 4.5 Discussion ...... 72
5. Discussion and future work ...... 83
APPENDIX ...... 87
A. Asymptotics for Chapter 1 ...... 88
BIBLIOGRAPHY ...... 93
vi LIST OF FIGURES
Figure
2.1 Averageη ˆm values from 100 simulations ...... 20
2.2 Estimates of functionη ˆ(·) from Eli Lilly data. Index values in the T plotted data are βˆ x, where βˆ comes from the constrained approach, and treatment effect estimates are the Z values from Virtual Twins procedure. Those points to the right of the vertical dotted line would be considered “enhanced” based on this analysis...... 25
3.1 Plot of True g(x) for Cases 1-4 ...... 45
3.2 Histogram of True g(x) for Cases 1-4 ...... 46
3.3 Histogram ofg ˆ(x) for TROPHY Data ...... 50
4.1 Rejection rates (α = 0.05) for simple linear model simulations . . . 66
4.2 Histograms of p-values for simple linear scenario 1 (β = 0.5, γ = 0.25, θ = 0.35)...... 74
4.3 Histograms of p-values for simple linear scenario 2 (β = 0.5, γ = 0.25, θ =0) ...... 75
4.4 Histograms of p-values for simple linear scenario 3 (β = 0.25, γ = 0.5, θ = 0.35)...... 76
4.5 Histograms of p-values for simple linear scenario 4 (β = 0.25, γ = 0.5, θ =0) ...... 77
4.6 Rejection rates (α = 0.05) for complex model simulations ...... 78
4.7 Histograms of p-values for complex scenario 1 (g(x) = 15I(x1 > 0, x2 > 0))...... 79
vii 4.8 Histograms of p-values for complex scenario 2 (g(xi) = 5) . . . . . 80
4.9 Histograms of p-values for complex scenario 3 (g(xi) = 5 + ei)... 81
4.10 Histograms of p-values for complex scenario 3 (g(x) = 0) ...... 82
viii LIST OF TABLES
Table
2.1 Simulation results: variable selection performance ...... 21
2.2 Performance of standard error estimates ...... 23
2.3 Estimates for Eli Lilly data ...... 26
3.1 Simulation study results: subgroup identification performance . . . 44
3.2 Simulation study results: Q(Aˆ) estimation performance ...... 47
4.1 P-values for TROPHY data ...... 71
ix CHAPTER 1
Introduction
In recent years, there has been a great deal of interest in using a patient’s specific information to make more informed treatment decisions. This practice, often referred to as personalized medicine, is motived by the fact that few treatments are equally effective for all individuals in a population. A treatment may be quite effective for some subset of a population, but mildly effective, ineffective, or even harmful for others. Because of this, there is great interest in identifying which individuals in a population, if any, will respond well to a treatment. More specifically, it is necessary to identify which characteristics, if any, lead to this enhanced response if one wishes to pursue a personalized treatment.
A generally accepted approach to identifying such characteristics is to pre-define a small number of subregions of the covariate space before looking at the data, and then evaluate them. However, one may not always know which subgroups to consider, and increasing the number of subgroups considered also increases the risk of false positive
findings, which is already a well-known danger in subgroup analysis. One way to reduce this risk of false positives is to employ a multiple testing approach, such as a
Bonferroni correction. This can effectively reduce false positives, but also decreases
1 2 the power to detect true subgroups.
An alternative approach, which will be the main focus of this dissertation, is to pre-define a statistical procedure for identifying subgroups [Ruberg et al., 2010].
These procedures can eliminate the need for a priori specification of subgroups, and may help to reduce the risk of false findings, though some risk still remains. Such procedures have been proposed by many authors, including Friedman and Fisher
[1999], Negassa et al. [2005], Su et al. [2008, 2009], Brinkley et al. [2010], Cai et al.
[2011], Foster et al. [2011], Lipkovich et al. [2011], Qian and Murphy [2011], Zhao et al. [2011], Imai and Ratkovic [2012] and Zhang et al. [2012]. When developing such a procedure, it is common to first consider what each subject’s potential outcome value would be, given each of the treatment options [Zhang et al., 2012]. That is, when two treatment options (say treatment 1 and treatment 0) are present, it is common to consider what each subject’s potential outcome would be given treatment
1 and what it would be given treatment 0. One general way to identify subgroups is to first estimate these two potential outcomes, and then take the difference, which is an estimate of the treatment effect. One can then investigate the relationship between these estimated treatment effects and the covariates to obtain subgroups.
Alternatively, one could attempt to identify subgroups by maximizing the expected response under a class of treatment regimes [Gunter et al., 2007, Zhang et al., 2012].
The treatment regimes in such a case will generally be defined based on the covariates, and will be of the form xi ∈ A ⇒ Ti = 1, xi ∈/ A ⇒ Ti = 0, where xi and Ti are the covariate vector and treatment indicator for subject i and A is some region of the covariate space. Thus, with this approach, the “optimal” subgroup is the region
A which maximizes the expected response when only individuals in A will receive treatment 1 and only individuals in region Ac will receive treatment 0. 3
Note that, in the setting of personalized medicine, the ultimate goal is to use the identified subregion to define “rules”, which can be used in the future to make more informed treatment decisions. Moreover, these treatment decisions will nearly always be made by someone such as a physician or nurse practitioner, who may only have a modest understanding of statistics. Thus, an issue which should be considered before employing any subgroup identification procedure is the potential form and complexity of the resulting subgroup(s), which can both vary considerably depending on which approach is taken. A very complex subgroup, which depends on some, or perhaps all of the available covariates will often be quite good at identifying truly enhanced responders, but such subgroups may lack “nice” interpretability. In addition, the dependence on a large number of covariates means a large amount of information will need to be collected before a treatment decision can be made, which could lead to slower, more expensive, or more invasive (due to performing of unnecessary procedures to collect information) treatment decisions than are necessary.
This could potentially limit the chances of such a subgroup being used in practice. In contrast, a very simple subgroup, perhaps depending on only one or two covariates, may less accurately identify enhanced responders, but will be easier to interpret, and will likely see more real-world use. Given this tradeoff between classification accuracy and interpretability, the most “ideal” subgroups may be those which are of only moderate complexity. To this end, we will focus on the identification of simple subgroups, which depend on only a few covariates, and have a very simple form. In many cases, such subgroups may be able to classify enhanced responders well, while still being nicely interpretable, and will thus be more likely to see real-world use.
Because a large number of covariates may often exist, identifying “useful” sub- groups which depend on only a few covariates will generally require some form of 4 variable selection. One simple way to do this is to use a regression tree, which splits the data into a number of regions of the covariate space (i.e. subgroups) [Negassa et al., 2005, Su et al., 2008, 2009, Foster et al., 2011, Lipkovich et al., 2011]. These regions contain individuals who are similar with regard to the response, and they are generally defined using only a subset of the available covariates. Alternatively, one could consider a more model-based approach to selecting covariates. In particular, one could consider some form of penalized regression. Potential penalty functions include the LASSO [Tibshirani, 1996], smoothly clipped absolute deviation (SCAD)
[Fan and Li, 2001] and adaptive LASSO [Zou, 2006] penalties. These penalty func- tions are designed to force the regression parameter estimates which correspond to
“useless” variables to zero, thereby removing these variables from the model. Thus, predicted values of the response of interest will be a function of a linear combination of a potentially small number of covariates.
As previously mentioned, most subgroup analysis carries with it some potential for false positive findings. Pre-defining a subgroup identification approach can help to reduce false positives, but in our experience, these methods also have a tendency to identify subgroups, even when no true enhanced subgroup exists. To further re- duce the potential for false findings, one may wish to evaluate the “usefulness” of a subgroup once it is identified, perhaps by performing a hypothesis test or computing some type of “enhancement” metric [Foster et al., 2011]. Before such a hypothesis test can be implemented, one must consider what “null” means in the setting of subgroup analysis. Note that “meaningful” subgroups arise when the treatment effect differs as covariate values differ. That is, subgroups arise when treatment-by-covariate in- teractions exist. Thus, in this setting, one could define “null” data as that in which treatment is constant with respect to the covariates, so that no treatment-by-covariate 5 interactions exist. Alternatively, if one has a specific subgroup to evaluate, “null” data could be defined as data for which the effect of treatment in the chosen subgroup is no different than that for the entire population. In this dissertation, we will consider the more general definitition that no treatment-by-covariate interactions exist.
In this dissertation, we will consider a number of methods which use randomized clinical trial data to identify simple subgroups of enhanced treatment effect, which should depend on only a small number of covariates. Using randomized clinical trial data allows us to avoid potential problems with confounded relationships, and thus have more confidence that the identified subgroup contains “truly” enhanced individ- uals. Moreover, randomized clinical trial data generally contains a large number of subjects, which is advantageous, as large samples are generally required if one wishes to accurately identify subgroups.
In Chapter 2, we consider the use of adaptive LASSO-penalized monotone single- index models to identify subgroups of enhanced treatment effect. A single-index model assumes that the outcome of interest is an unknown function of a linear combination of covariates. By forcing this unknown function to be monotone, we are able to nicely describe the estimated effect of each covariate on the response of interest. In addition, by penalizing the regression parameter, the resulting model will generally depend on only a relatively small number of covariates, making it easier to interpret.
In Chapter 3, we propose a two-stage subgroup identification procedure, which can be viewed as a model-based alternative to Virtual Twins [Foster et al., 2011]. In the first stage of this procedure, we use nonparametric regression to obtain treatment effect estimates for each subject. From these estimates, we define a criterion [Sutton and Barto, 1998, Gunter et al., 2007], which is subsequently used to systematically evaluate many subgropus of a simple, pre-specified form. The identified subgroup is 6 that which has the best value of the evaluation criterion. In this chapter, we also consider the use of an enhancement metric [Foster et al., 2011] to evaluate the utility of identified subgroups.
In Chapter 4, we propose a number of permutation-based methods for obtaining p-values for treatment-by-covariate interactions, which can be used to test whether or not an identified subgroup is truly enhanced. These methods are used to obtain p-values for some of the enhancement metric estimates discussed in Chapter 3. All methods in this dissertation are evaluated in simulation studies, and illustrated using randomized clinical trial data.
In Chapter 5, we present an overall discussion of the proposed methods, and consider a number of potential extensions and modifications of these methods. CHAPTER 2
Variable selection in monotone single-index models via the adaptive LASSO
2.1 Introduction
Linear regression is a simple and commonly-used technique for assessing rela-
tionships of the form y = βT x + between an outcome of interest, y, and a set of
covariates, x1, . . . , xp; however, in many cases, a more general model may be desirable.
As noted by Hardle et al. [1993], one particularly useful and more general variation of the linear regression formulation is the single-index model
T yi = η(β xi) + i, (2.1)
T where xi’s are subject-specific covariate vectors, β = (β1, . . . , βp) , yi ∈ R, η is
2 an unknown function, 1, . . . , n are iid errors with mean zero and variance σ , and
i’s and xi’s are independent. To ensure identifiability, no intercept is included, and β1 is assumed to be equal to 1. These models are able to capture important features in high-dimensional data, while avoiding the difficulties associated with high- dimensionality, as dimensionality is reduced from many covariates to a univariate
7 8 index Yu and Ruppert [2002]. Single-index models have applications to a number of
fields, including discrete choice analysis in econometrics and dose-response models in biometrics Hardle et al. [1993].
There is a rich literature on estimation of β and η, including Hardle et al. [1993],
Yu and Ruppert [2002], Ichimura [1993], Carroll et al. [1997], Xia et al. [2002], Xia and Hrdle [2006], among many others. Additionally, variable selection for single-index models was considered by Kong and Xia [2007], who proposed the separated cross- validation method, and Liang et al. [2010], who applied the smoothly clipped absolute deviation (SCAD) approach to partially linear single-index models. However, little consideration has been given to such problems for monotone single-index models, where η is required to be non-decreasing (or non-increasing). In the case of linear models, a great many authors, including Tibshirani [1996], Fan and Li [2001], Zou
[2006] and Zou and Zhang [2009] have considered variable selection via penalized least squares, which allows for simultaneous selection of variables and estimation of regression parameters. Several penalty functions, including the SCAD Fan and Li
[2001], the adaptive LASSO Zou [2006] and the adaptive elastic-net Zou and Zhang
[2009], have been shown to possess favorable theoretical properties, including the oracle properties; that is, consistency of selection and asymptotic normality, with the asymptotic covariance matrix being the same as that which would be obtained if the true underlying model were known. Hence, for large samples, oracle procedures perform as well as if the true underlying model were known in advance. Furthermore,
Liang et al. [2010] established the oracle properties for the SCAD for partially linear single-index models. Given the desirable properties of the SCAD, adaptive LASSO and adaptive elastic-net approaches, it is natural to consider the extension of these methods to monotone single-index models. Unlike the adaptive LASSO and adaptive 9 elastic-net, which present a convex optimization problem, the SCAD optimization problem is non-convex, and thus more computationally demanding Hastie et al. [2009].
In addition, the adaptive elastic-net and SCAD methods require the selection of two tuning parameters, whereas the adaptive LASSO requires the selection of a single tuning parameter. Therefore, for convenience, computational efficiency, and because covariates in our example data are not highly correlated (a condition under which the adaptive elastic-net is especially good), we consider adaptive LASSO penalized least squares estimation of β in monotone single-index models.
The assumption of monotonicity and the desire to select a subset of the covari- ates are motivated in part by the randomized clinical trial data considered in Foster et al. [2011]. A monotonicity assumption is often reasonable, and such an assumption may improve prediction and reduction in model complexity, while also allowing for more straightforward inference. Foster et al. Foster et al. [2011] consider methods for subgroup identification in randomized clinical trial data. In such cases, should a subgroup be identified, it is desirable that this subgroup be easily described, and depend on only a small number of covariates. Application of the methods proposed ˆ ˆ T in this paper result in estimatesη ˆ and β, such thaty ˆi =η ˆ(β xi), whereη ˆ is mono-
tone and βˆ generally includes a number of zero values. Using this model, one can
classify individuals withy ˆ’s beyond some predefined threshold, c, as being in the
subgroup. Then, because of the monotonicity ofη ˆ, the predefined threshold can be
T converted into an equivalent threshold, c0, on βˆ x, and the impact of the chosen co- variates on subgroup membership can be easily described. Without the assumption of monotonicity, the subgroup may be a collection of several disjoint subregions of the covariate space, making each covariate’s impact on subgroup membership more difficult to ascertain. 10
The remaining sections of this article are as follows. In Section 2, we consider
penalized least-squares estimation for monotone single-index models, briefly discuss
asymptotics, and discuss a method to obtain standard error estimates for β. In
Section 3, we present the results of a simulation study implemented to assess the
performance of the adaptive LASSO penalized single-index models. In Section 4, we
briefly discuss the application of this method to the randomized clinical trial data,
and in Section 5, we give concluding remarks.
2.2 Estimation for monotone single index models
Our estimation procedure iterates between estimation of β and η until conver-
gence. Given some η, the penalized least-squares estimator of β can be found by
minimizing
n p X T 2 X Q(β) = yi − η(β xi) + λn wj|βj|, (2.2) i=1 j=2
where wj, j = 2, . . . , p are known weights and covariates xi are standardized to have
mean zero and variance 1. Due to the identifiability constraint specified in model
ˆ −γ (2.1), β1 is not penalized. Following Zou [2006], we choose wj = |βinit,j| for γ > 0,
ˆ α 1 where βinit is a n -consistent estimator of β, where 0 < α ≤ 2 . We use linear ordinary ˆ least squares (OLS) estimates for βinit, as under the assumptions of Theorem 2.1 in Li √ and Duan [1989], these are shown to be n-consistent up to a multiplicative scalar. ˆ ˆ Once obtained, βinit is rescaled by β1,init. Alternatively, weights could be defined
using the unpenalized single-index model estimates of β.
For a given β, without considering the monotonicity constraint, η can be estimated 11
at some point t using the Nadaraya-Watson kernel-weighted average:
T P t−β xj j yjK h ηˆ(t; β, y, X, h) = , (2.3) T P t−β xj j K h
where X is the covariate matrix, K is a fixed kernel function and h is a bandwidth.
Note that, when β is known,η ˆ is determined by h, so a value of h must be chosen. We consider kernel functions which are symmetric probability densities. For numerical stability, we hold (2.3) fixed for all t outside the range of the βT x’s. That is,η ˆ(t) =
T T T T ηˆ(mini(β xi)) if t < mini(β xi) andη ˆ(maxi(β xi)) if t > maxi(β xi).
Combining (2.2) and (2.3), the adaptive LASSO estimator for β is obtained by minimizing
p ˆ X0 T 2 X Q(β, h) = yi − ηˆ(β xi; β, y, X, h) + λn wj|βj| (2.4) i j=2
P0 with respect to β, where i denotes summation over i such that the denominator in the kernel estimator is not too close to zero. Details can be found in Hardle et al. ˆ [1993]. With the inclusion of the penalty term in (2.4), β becomes a function of λn, ˆ so in addition to h, a value of λn must be chosen if β is to be obtained. Throughout this paper, we refer to the method of estimating β and η without a monotonicity constraint, using objective function (2.4), as the unconstrained approach.
2.2.1 A smooth monotone function estimate for η with fixed β
There are a variety of ways to obtain smooth monotone regression function es- timates, including quadratic B-splines He and Shi [1998], I-splines Ramsay [1988], empirical distribution tilting Hall and Huang [2001], the scatterplot smoothing ap- 12
proach of Friedman and Tibshirani [1984], and the kernel-based approach of Mukerjee
[1988] and Mammen [1991]. We consider the kernel-based method of the latter two
papers, which we briefly describe below.
Assume β is known. The proposed monotone estimatorη ˆm requires two steps:
Isotonization. This step involves the application of the pooled adjacent violator
T algorithm (PAVA) Barlow et al. [1972]. Using (β xi, yi) ordered by increasing
T β xi as data, PAVA produces monotone estimatesm ˆ 1,..., mˆ n, which are av-
erages of yj’s near i (unless y’s are already monotone, in which casem ˆ i = yi),
and which are not necessarily smooth Friedman and Tibshirani [1984].
Smoothing. Apply the kernel estimator (2.3) with yi replaced bym ˆ i for all i to
estimate η. That is,η ˆm(t) =η ˆ(t; β, mc, X, h).
Sincem ˆ 1,..., mˆ n are monotone, the resulting function estimate is monotone in t. It is worth noting that this may not necessarily be the case for other smoothing methods, such as local linear regression.
As previously mentioned, a bandwidth is needed to estimate η, and can be found using cross-validation; however, our algorithm requires estimation of both η and its derivative η0, so care must be taken. In particular, to ensure good algorithmic con- vergence, it is crucial thatη ˆ0 be smooth, but to obtain a smooth estimate of η0, it is often necessary to oversmooth η. Thus, we restrict the range of potential bandwidths in our cross-validation. Specifically, h is restricted to be between 0.1∗sd(Xβ) and sd(Xβ), as values in this range were found to perform well in our simulations. 13
2.2.2 Estimation for β with fixed η
The shooting algorithm proposed by Fu [1998] has been shown to perform well in solving LASSO penalized least-squares problems for linear models Friedman et al.
[2007]. Therefore, we consider the application of this algorithm to LASSO problems for the single-index model. One way to achieve this is to employ a linear approxi-
T T mation via Taylor series expansion of η(β xi) about β0 xi, where β0 is known. We define the linear approximation as follows:
T T 0 T T T η β xi ≈ η β0 xi + η β0 xi β xi − β0 xi . (2.5)
Let
∗ T 0 T T yi = yi − η β0 xi + η β0 xi β0 xi and
∗ 0 T xi = η β0 xi xi.
Then we have
T T 0 T T T ∗ T ∗ yi − η β xi ≈ yi − η β0 xi − η β0 xi β xi − β0 xi = yi − β xi , and (2.4) can be approximated by
p ˆ X0 ∗ T ∗2 X Qlin (β) = yi − β xi + λn wj|βj|, (2.6) i j=2 14
which is a LASSO penalized least-squares problem for the linear model, and can thus
be solved using the shooting algorithm.
Note that (2.5) involves an estimate of η0. This estimate is obtained as fol-
T n lows. Sort the observations by increasing β0 xi, and define new data (x˜i, y˜i):
o T T η(β0 xi+1)−η(β0 xi) xi+1−xi , i = 1, . . . , n − 1 , wherey ˜i = T T , and x˜i = xi + . This β0 xi+1−β0 xi 2 0 T new data should “look like” data coming from the modely ˜i = η (β xi) + ˜i, so
0 n o η (t) can be estimated using (2.3), but with (xi, yi): i = 1, . . . , n replaced by n o 0 ˜ ˜ ˜ (x˜i, y˜i): i = 1, . . . , n − 1 , i.e.η ˆ (t) =η ˆ(t; β, y˜, X, h), where h is a new bandwidth for the derivative estimate. To select h˜, cross-validation can again be used.
2.2.3 Algorithm
The algorithm to obtain final estimates of η and β iterates between the steps
(k) (k) in Sections 2.1 and 2.2 until convergence. After k iterations, let βˆ ,η ˆm and
(k) (k) mˆ 1 ,..., mˆ n denote the current estimates of β and η and the current PAVA es- timates respectively. For a given λn, the “final” estimates of β and η are obtained as follows:
n ˆ (k)T o 1. Using data (β xi, yi): i = 1, . . . , n , apply PAVA to obtain new monotone n ˆ (k)T (k+1) o data (β xi, mˆ i ): i = 1, . . . , n , and define the monotone function esti-
(k+1) n ∗ (k) mateη ˆm (t) using (2.3). Select h via a grid search on values 0.1 sd(Xβˆ ),
(k) (k) o 0.2∗sd(Xβˆ ), . . . , sd(Xβˆ ) using leave-one-out cross-validation. For com-
putational convenience, fix h after a small number, say a, of iterations (i.e.
when k = a ).
n ˆ (k)T (k+1) o 2. Using data (β xi, mˆ i ): i = 1, . . . , n , obtain the derivative data n (k)T o ˆ (k+1) (k+1)0 (β x˜i, y˜i ): i = 1, . . . , n − 1 , and define the derivativeη ˆ (t) using 15
n (k) (k) (k) o (2.3). Select h˜ from the grid 0.1∗sd(Xβˆ ), 0.2∗sd(Xβˆ ), . . . , sd(Xβˆ )
using leave-one-out cross-validation. As with h, h˜ is fixed after a iterations.
3. Let the general notation z(kl) indicate the lth update to z(k). Using approxima- n ∗(k1) ∗(k1) o ˆ(k1) tion (2.5), obtain data (xi , yi ): i = 1, . . . , n , and minimize Qlin (β) (k1) from (2.6), giving βˆ . Repeat this step m−1 more times, for a total of m itera-
(km) (k+1) tions, each time updating the linear approximation (2.5), so that βˆ ≡ βˆ
n ∗(km) ∗(km) o n ∗(k+1) ∗(k+1) comes from data (xi , yi ): i = 1, . . . , n ≡ (xi , yi ): i = o 1, . . . , n .
(k+1) (k) ˆ ˆ 4. Cycle through steps 1-3 until β −β becomes smaller than a prespecified precision level. The final estimate of η is then obtained by implementing step
1 once more using the converged β estimate.
ˆ (k) ˆ(k) The identifiability constraint is imposed by rescaling β by β1 each time Step 3 is completed, so it is desirable that β1 be nonzero to avoid potential numerical problems.
To help ensure this in practice, one could first fit a linear model, and choose the largest
(or most significant) βj estimate to be that which is subsequently unpenalized and forced to be 1. If in the final model another coefficient is larger, then one could re-run the analysis with that coefficient being the one which is upenalized and forced to be
1. As suggested by one of the reviewers, one could also consider a sensitivity analysis in which multiple models were fit, each time forcing a different coefficient to be 1. ˆ A value of λn must be chosen before β can be estimated. Suppose that β(λn) andη ˆm(t; λn) are the estimates of β and η(t), given tuning parameter λn. To choose a value of λn, we use the Bayes information criterion (BIC) measure of Liang et al. 16
[2010]. Specifically, we choose the value of λn that minimizes:
2 n 1 X0 o log(n) BIC(λ ) = log y − ηˆ (βˆ(λ )T x ; λ ) + DF , n n i m n i n n λn i
ˆ ˆ where DFλn is one less than the number of non-zero values in β(λn), since β1 is forced to be nonzero. To find the optimal λn, a grid search is employed.
In the remaining sections, the monotone-constrained method described above is referred to as the constrained approach.
2.2.4 Asymptotics
Using the results of Hardle et al. [1993] and arguments similar to Zou [2006], it is possible to establish the oracle properties for the unconstrained approach. We provide an outline of such an argument here.
Suppose the regularity conditions of Hardle et al. [1993] hold. Then, by their main theorem, we can rewrite the sum of squares portion of (2.4) as a sum of three terms,
S˜, T , and R, where S˜ and T depend only on β and h respectively, and the remainder term R is negligible. Thus, as S˜ is the only term which depends on β, (2.4) can be T p n 1/2 o n 1/2 ˜ P √σ reduced to S(β) + λn j=2 wj|βj| = n W 0 (β − β0) − n Z W 0 (β − β0) −
o p √σ P n Z + λn j=2 wj|βj|, where W 0 is a p × p matrix, β0 is the true index parameter,
√λn and Z is an asymptotically normal N(0, I) p-vector. Now suppose that n → 0, and
(γ−1)/2 3 √u λnn → ∞, where γ ∈ (0, 5 ], and let β = β0 + n , where k uk ≤ C. From here, following arguments very similar to Zou [2006], the oracle properties can be established. Two theorems and a formal proof for the unconstrained approach are given in the Appendix.
It seems that the oracle properties will also hold for β estimates from the con- 17
strained approach under certain conditions. Specifically, under the conditions of
−8/15 Theorem 2 in Mammen [1991], we haveη ˆm(t) =η ˆ(t) + Op(n ), for all t, whereη ˆm is our monotone estimator of η andη ˆ is the Nadaraya-Watson kernel-weighted aver- age. Thus, it is possible to reduce the penalized sum of squares for the constrained approach to (2.4) plus a negligible remainder term. The oracle properties for the constrained approach would hold by the same reasoning used for the unconstrained approach.
In practice it is difficult to verify that the conditions needed for the theory hold.
Because a data-driven method (BIC) is used to select the tuning parameter, λn, we
√λn cannot guarantee the required rate of convergence. Thus, the assumptions n → 0
(γ−1)/2 and λnn → ∞ may not hold.
2.2.5 Bootstrap standard errors
Standard errors for our β estimates can be obtained via the bootstrap. In partic-
ular, for a given data set, we employ the adaptive LASSO-based residual bootstrap
(ARB) approach discussed by Chatterjee and Lahiri [2011] to obtain many, say M,
bootstrap data sets. A penalized single-index model is then fit on each of these boot-
strap data sets, giving M sets of estimates. The estimated standard errors are then
obtained by taking the standard deviations of the M estimates for each βj.
For a given data set, we obtain a residual bootstrap data set as follows. Suppose ˆ ˆ T β andη ˆ are final estimates of β and η for a particular data set. Let ei = yi −ηˆ(β xi),
i = 1, . . . , n be the residuals for this data set. A residual bootstrap data set is then
ˆ T ∗ ∗ ∗ obtained by replacing yi withη ˆ(β xi) + ei , i = 1, . . . , n, where {e1, . . . , en} is a
1 Pn random sample (drawn with replacement) from the centered residuals, ei − n i=1 ei, i = 1, . . . , n. The covariate matrix remains the same across the bootstrap data sets. 18
Based on additional simulations (results not given), creating residual bootstrap data sets using permuted (sampled without replacement) residuals gives nearly iden- tical results to those shown in Table 2.2. As noted by one reviewer, in practice, the interpretation for the standard errors can be awkward, particulary in cases where a number of covariates are highly correlated. In such cases, one might expect the dis- tribution of these estimates to be a mixture of a continuous distribution and a point mass at zero. Thus, the estimates are a product of both selection and estimation, which can make interpretation difficult. This may be due to the known shortcomings of the adaptive LASSO for highly correlated predictors. If one believes that a number of covariates may be highly correlated, an alternative approach, such as the adaptive elastic-net, may perform better, and may lead to bootstrap standard error estimates based on a smaller number of zeros.
We generally suggest that one reselect λn with each bootstrap data set; however, our simulations (results not shown) suggest that holding λn fixed across bootstrap data sets gives standard error estimates which are nearly identical to those found by reselecting λn for each bootstrap data set. Thus, it may be reasonable to consider
fixed-λn bootstrap standard errors if reselecting λn for each bootstrap data set is too computationally burdensome.
2.3 Simulations
A simulation study was performed using R software to evaluate the performance of the proposed methods. To comply with the conditions in Section 2.4, a value of
3 5 was chosen for γ for adaptive LASSO. Additionally, for each example, a large test set (n = 10, 000) was generated, and final β estimates from each of the simulated 19
data sets were used to calculate the mean squared error (MSE) for this large test set.
To evaluate the performance of all methods considered, we recorded the number of ˆ ˆ correct and incorrect zero values in β, as well as the total proportion of βj’s correctly estimated as zero or non-zero for each data set. The average of these proportions across all simulated data sets is referred to in Table 2.1 as the relative frequency correct. We also computed the false discovery rate (FDR), which is the percentage of non-zero βˆ values which should have been zero. For each data set, the optimal tuning parameter value λn was chosen from the grid {0, 0.01,..., 0.25} using BIC.
2.3.1 Examples
For all simulations, 100 data sets of size 100 were generated from the model
T 3 yi = (β xi) + i,
1 1 where xi’s were Unif[− 2 , 2 ], and error terms were normal with mean zero and vari- ance σ2. We considered five different cases:
T (i) β = (1, 0.8, 0, 0, 0, 0, −0.7, 0, 0, 0) , xi’s independent, and ’s independent with
σ = 0.20;
(ii) Same as case (i), but with σ = 0.30;
(iii) Same as case (i), but with β changed to (1, 0.8, 0, 0, 0, 0, −0.2, 0, 0, 0)T ;
(iv) Same as case (i), but with Corr(xij, xik) = 0.5, j 6= k;
(v) Same as case (i), but with an additional 50 noise covariates, so that β =
T (1, 0.8, 0, 0, 0, 0, −0.7, 0, 0, 0, 01×50) . 20 0.2 0.1 0.0 Response −0.1 −0.2 Truth Monotone SIM 90% Conf. Bands −0.3
−0.6 −0.4 −0.2 0.0 0.2 0.4 0.6
Estimated Index Value
Figure 2.1: Averageη ˆm values from 100 simulations
From Table 2.1, we can see that, in all cases, the constrained approach shows noticeably better reduction in model complexity and smaller FDR than the uncon- strained approach. Additionally, the constrained approach has mean test MSEs which are smaller, and closer to the corresponding oracle test MSEs than the unconstrained approach. Reduction in model complexity for the constrained approach appears to be reasonably insensitive to the changes in simulation settings considered above; how- ever, the unconstrained approach appears to suffer in this regard, especially when true parameter values are decreased or error standard deviation is increased. 21
Table 2.1: Simulation results: variable selection performance
Rel. Freq Avg. No. βˆ = 0* Mean Test Method Correct Correct Incorrect FDR MSE (×100)
Case (i)1 Cons.: 0.92 6.22 0.00 0.21 4.93 Uncons.: 0.85 5.47 0.01 0.34 5.63 Cons. oracle: 1.00 7.00 0.00 0.00 4.74 Uncons. oracle: 1.00 7.00 0.00 0.00 4.96
Case (ii)2 ** Cons.: 0.89 6.09 0.17 0.24 10.87 Uncons.: 0.75 4.68 0.16 0.45 12.84 Cons. oracle: 1.00 7.00 0.00 0.00 10.07 Uncons. oracle: 1.00 7.00 0.00 0.00 10.56
Case (iii)3 Cons.: 0.86 6.25 0.65 0.24 4.64 Uncons.: 0.73 4.83 0.56 0.47 5.51 Cons. oracle: 1.00 7.00 0.00 0.00 4.45 Uncons. oracle: 1.00 7.00 0.00 0.00 4.65
Case (iv)4 Cons.: 0.88 6.15 0.32 0.24 4.79 Uncons.: 0.82 5.45 0.27 0.36 5.38 Cons. oracle: 1.00 7.00 0.00 0.00 4.51 Uncons. oracle: 1.00 7.00 0.00 0.00 4.78
Case (v)5 Cons.: 0.94 53.70 0.10 0.53 5.64 Uncons.: 0.87 49.36 0.13 0.74 7.16 Cons. oracle: 1.00 57.00 0.00 0.00 4.74 Uncons. oracle: 1.00 57.00 0.00 0.00 4.96 Note: “oracle” indicates true zero β values known. η is estimated in all methods. * Average number of variables dropped in final model. 1 T β = (1, 0.8, 0, 0, 0, 0, −0.7, 0, 0, 0) , Corr(xij, xik) = 0, j 6= k, σ = 0.20. 2 3 Same as Case (i), but σ = 0.3. Same as Case (i), but β7 = −0.2. 4 Same as Case (i), but Corr(xij, xik) = 0.5, j 6= k. 5 T Same as Case (i), but β = (1, 0.8, 0, 0, 0, 0, −0.7, 0, 0, 0, 01×50) . ** Required 101 simulated data sets due to numerical problems. 22
Additional simulations were implemented to evaluate the performance of the pro-
posed methods under alternative monotonic functions, η (results not shown). In
particular, we considered a linear function, and two spline functions; one resembling
the cubic function from the above examples, but with two knots chosen to create a
wider “flat” section around the origin, and one which is constant to the left of the
origin and quadratic to the right. As expected, both methods performed well in the
linear case. In the cubic spline case, reduction in model complexity was good, but
mean test MSE became noticeably larger, and in the case of the constant spline with
the quadratic knot, mean test MSE was good, but reduction in model complexity was
noticeably worse. Thus, as one might expect, the proposed methods are less useful
in cases where η contains large sections which are nearly flat, or exactly constant.
To evaluate the performance of our standard error estimates, residual bootstrap
standard errors (based on 100 bootstrap data sets) were calculated for case (i) above.
Let SD denote the standard deviation of the 100 βj estimates, j = 1, . . . , p. Addition- ally, let SE and SEsd denote the mean and the standard deviation of the 100 estimated
SE’s respectively. Looking at Table 2.2, we can see that the standard error estimates appear to perform reasonably well, though they sometimes slightly underestimate or overestimate the true values.
To demonstrate the ability of penalized monotone single-index models to capture non linear relationships, we computedη ˆm values across a fine grid of input values and averaged theseη ˆm’s across the 100 data sets in case (i). These average values can be found in Figure 2.1, along with the true function η and 90% empirical pointwise confidence bands forη ˆm. As we can see, the monotone function estimateη ˆm appears to closely follow the true function. 23
Table 2.2: Performance of standard error estimates
ˆ ˆ β2 β7
Method SD SE (SEsd) SD SE (SEsd)
Cons.: 0.25 0.20 (0.08) 0.20 0.18 (0.06) Uncons.: 0.28 0.34 (0.41) 0.28 0.27 (0.26) Note: required 102 simulated data sets due to nu- merical problems.
Because we are interested in using the proposed methods to identify subgroups, we also compared “enhancement” classification between the two methods for case (i).
For this comparison, we consider a subject to be enhanced if η(xT β) > 0. On aver- age, 88% of subjects identified as enhanced by the constrained approach were truly enhanced, whereas for the unconstrained approach, only 73% were correctly identified on average. Thus, the constrained approach may be advantageous for applications to subgroup identification.
The two methods methods require approximately the same amount of time to complete a single iteration of our algorithm for a given value of λ. However, for some data sets, the constrained approach requires more iterations to achieve the same degree of convergence as the unconstrained approach. For example, for case (i) of our simulations, the median run time for a data set for the constrained approach was approximately 64% longer than that for the unconstrained approach.
2.4 Example data
In this example, we apply the proposed methods to the Eli Lilly data in Foster et al.
[2011], which come from a randomized, double-blinded clinical trial in patients with a 24
critical illness in the ICU conducted over a decade ago. We consider 1019 individuals,
of whom 512 received the experimental treatment in addition to the standard of care.
The remaining patients received placebo with the standard of care. The intervention
is a drug that is intended to improve survival in patients with a critical illness, and
the endpoint was survival at 28 days post-randomization to treatment/placebo. We
consider 58 covariates analyzed by Foster et al. [2011], which include demographic,
laboratory, medical history and questionnaire data. Of these, 9 are binary, 22 are
regarded as continuous, and 27 are dummy variables coming from subdivision of 12
categorical variables.
In Foster et al. [2011], a random forest was used to obtain two predicted prob- ˆ ˆ abilities, P1i and P0i, for each individual, where P1i is the probability of survival at
28 days post-randomization for subject i if that individual had received treatment and P0i is that if subject i had received placebo. The estimation of these prob- abilities was motivated by the fact that the methods of Foster et al. [2011] were designed to identify subgroups of enhanced treatment effect in randomized clinical trial data. Therefore, a new outcome representing the treatment effect for person i, ˆ ˆ Zi = P1i − P0i, i = 1, . . . , n, was subsequently defined, since individuals in such a
subgroup should ideally have values of P1i which are much larger than P0i. Then, a
single regression tree was fit using Z as the outcome and the covariates as predictors.
This tree identified subgroups of enhanced treatment effect which depended on age
at admission, baseline creatinine clearance, baseline interleukin 6 and hypertension
(yes, no or unknown). This method was referred to by Foster et al. [2011] as “Virtual
Twins.”
Using Z as the outcome and the 58 covariates as predictors, we fit penalized
single-index models with and without monotonicity constraints. All covariates were 25
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0.4 ● ● ● ● ● ● ● ●● ●● ● ●● ● ● ● ●●● ● ● ● ● ● ● ● ● ● ● ● ●●● ●● ●● ● ●● ● ●●● ● ● ● ● ● ● ● ● ●●●●● ● ● ● ● ● ●● ●● ● ●● ● ● ● ● ● ●● ● ●● ● ●● ● ● ● ● ● ● ●● ● ●● ●●●●●● ● ● ● ● ●● ●●●● ●●● ● ● ● ● ● ● ● ●●●●● 0.2 ● ●● ● ● ● ● ● ●●● ●●● ● ● ● ● ●●●●●● ● ● ● ● ●● ●● ● ● ● ●● ●●●●●●● ● ●● ● ● ● ● ● ● ●● ●●●● ●●●●●●●● ●●●●●● ● ● ● ●●● ● ●● ● ●●●● ● ●●● ● ● ●● ● ●● ●●● ●●●● ●●●● ●●● ●●● ● ● ●● ●●●● ●● ● ●● ●●●●●●●● ● ● ● ● ●●●● ●●●●●●● ●● ●●● ●● ●● ●● ●● ● ● ● ● ● ● ●●●● ●● ●●●● ●● ●● ● ● ● ● ●●●●●●●●●●●●●● ●●● ●●● ●● ● ● ● ●● ●● ●● ●●●● ●● ● ●●●● ●●●● ●●●●●●●●● ●● ● ● ● ● ● ●●● ● ●●●●● ●●●●●●●●● ●●● ● ●●●● ● ● ● ● ●●●●●●● ●●●● ● ●●● ●● ● ● ● ● ● ● ●●● ● ●●● ● ●●●●●●●● ● ● ● ● ● ●● ● ●●●● ●● ●● ●●●●● ●●●●●●●●● ● ● ● ●●● ● ●●●●●●●●● ●●●● ●●●●● ●●●● ● ●● ● ● ● ● ●● ●●●●●●●●●●●●●● ●●● ●● ●●● ●●●● ● ● ● ● ● ● ●● ● ●●● ●●●●●●●●●● ● ●● ●● ● ●● ●●●● ●● ● ● ●● ●●●●●●●●●●●●● ● ● ● ● ● ● ● ●● ● ●●●● ●●●●●●●● ● ● ●●● ● ●● ● ●●●●●●●● ● ● ● ● ● ● ● ●● ●● ● ●●●● ● ● ●●●●● ●●● ●● ● 0.0 ● ● ●● ● ● ● ● ● ● ●● ●●●● ●●●● ● ●● ● ● ● ●● ●● ●●● ●●● ● ● ● ●●●● ● ● ● ● ● ●●●● ● ●● ●● ●●● ●● ●●● ● ● ● ● ● ● ● ● ● ●●● ● ●●●●●● ● ●● ●● ● ● ● ● ●● ● ●●● ●● ● ● ● ●● ● ●● ●● ●● ● ●●● ● ● ●● ● ● ● ● ● ● ●● ● ● ●● ● ● ●● ● ●● ●● ●● ●● ●● ● ● ● ● ● ●●● ● ● ●● ●●●● ● ● ● ● ● ● ● ●● ● ● ● ●● ● ●● ● ●● ● ● ●● ● ●● ●● ● ● ● ●● ●●● Estimated Treatment Effect Estimated Treatment ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●● ● ● ● ●● ● ● ● ● −0.2 ● ● ● ● ● ● ● Monotone ● Unconstrained −0.4
−6 −4 −2 0 2 4
Estimated Index Value
Figure 2.2: Estimates of functionη ˆ(·) from Eli Lilly data. Index values in the plotted T data are βˆ x, where βˆ comes from the constrained approach, and treatment effect estimates are the Z values from Virtual Twins procedure. Those points to the right of the vertical dotted line would be considered “enhanced” based on this analysis. standardized in this analysis due to large differences in scale, and age at admission was chosen to be the first column of X, as its corresponding initial estimate was the ˆ largest and most significant value of βinit It should be noted that this analysis was also performed with baseline creatinine clearance as the first column (results now shown), and the same six additional covariates were chosen, along with one other. The relative magnitude of the coefficients in this analysis were similar for most variables. Results from these models (with age at admission as first column of X) can be found in Table 26
2.3. Estimates for the constrained and unconstrained approaches were fairly similar,
though an additional covariate, baseline index of independence in activities of daily
living (ADL) Katz and Akpom [1976], was included by the constrained approach.
Table 2.3: Estimates for Eli Lilly data
Unconstrained Constrained Variable Estimate SE Estimate SE
Age 1.00 - 1.00 - ADL1 - - -0.13 0.04 Platelet Count -0.12 0.03 -0.19 0.08 Creat. Clear. -0.70 0.17 -0.81 0.21 Interleukin 6 0.60 0.11 0.70 0.13 # Organ Fail. 0.14 0.06 0.23 0.11 APACHE II2 0.24 0.09 0.33 0.14 1 Baseline index of independence in activities of daily living. 2 Pre-infusion acute physiology and chronic health evalua- tion II score.
In addition to β estimates, we computed bootstrap standard errors using 300
bootstrap samples. Because less important covariates will tend to be removed from
the model in most bootstrap samples, resulting in many zero bootstrap estimates, we
expect such covariates to have very small bootstrap standard errors.
The six covariates selected by both methods were age at admission, baseline cen-
tral lab platelet count, baseline creatinine clearance, baseline interleukin 6 (log scale),
number of baseline organ failures, and pre-infusion acute physiology and chronic
health evaluation II (APACHE II) score, of which age at admission, creatinine clear-
ance and interleukin 6 were also selected by the Virtual Twins method. Plots of the
data (from the constrained approach) and the final η estimates can be found in Figure
2.2. We can see that both estimates of η are reasonably close, with the constrained estimate being noticeably more smooth. From Figure 2.2, we can see that the pre- 27
T dicted region of enhanced treatment effect consists of βˆ x values which are larger
T than approximately −2, with the degree of enhancement increasing as βˆ x becomes larger. The constrained and unconstrained approaches identified 847 and 864 sub- jects as being enhanced, respectively, and of the 864 identified by the unconstrained approach, 845 were also identified by the constrained approach. Furthermore, for the constrained model, older individuals and those with higher baseline IL-6 respond very well to treatment, and patients with lower baseline creatinine clearance show a greater treatment differential. The findings from this analysis are reasonably consistent with the original conclusions from this trial, which suggested that patients who had higher risk factors for mortality responded better to the treatment.
As both fits suggest a relationship which is close to linear, an adaptive LASSO penalized linear model was also fit (results not shown), once using the default tuning parameter selection settings (10-fold cross-validation using squared error loss) in the
R glmnet package, and once using BIC to select the tuning parameter. The model resulting from the default tuning parameter selection settings contained 24 covariates, while the model selected using BIC contained 7 covariates. Although BIC is known to give smaller models than cross-validation, this dramatic difference in model com- plexity was mildly surprising to us. Based on the results of the linear model (using
BIC), it appears that the single-index models may not have added much compared to a linear model in this case.
2.5 Discussion
We proposed the use of adaptive LASSO variable selection for monotone single- index models, and showed that it performs well in a variety of situations. The con- 28
strained approach noticeably outperformed the unconstrained, and has the advantage
of more straightforward interpretation. A linear approximation to η via Taylor series was also proposed, thus allowing for the use of standard LASSO algorithms, such as coordinate descent, which have been shown to perform well. In addition, we suggested the use of residual bootstrap standard errors for β estimates, and showed that they perform reasonably well in simulations.
We argue that the unconstrained adaptive LASSO penalized single-index model estimates possess the oracle properties when η is estimated using the Nadaraya-
Watson formula. Additionally, we briefly argue that, following the results of Mammen
[1991], the oracle properties may also hold for the constrained approach, and it would be interesting to investigate this more formally. Furthermore, the proof outlined in √ Section 2.4 assumes that β is in a n-neighborhood of the true value, which is likely √ true given that the initial estimator of β is in a n-neighborhood of β0.
Our method of obtaining a monotone function estimate is very similar to that of
Friedman and Tibshirani [1984]. They suggested that it may be possible to improve
the estimation of the monotone penalized single-index model if one considers “one-
step” monotone function estimates, such as those suggested by He and Shi [1998] and
Ramsay [1988]. This is worthy of further investigation.
The adaptive LASSO penalty was chosen for convenience; however, one may wish
to consider other penalty functions. For instance, as noted by a reviewer, the adaptive
elastic-net can often outperform the adaptive LASSO approach, particularly when
covariates are highly correlated. Note that the linear approximation to the function
η does not involve the penalty function. Thus, the proposed method and algorithm
could easily be modified if one wished to use a different penalty function, such as the
SCAD or adaptive elastic-net. CHAPTER 3
Selection of simple rules for treatment assignment using patient information
3.1 Introduction
Though some treatments may be more widely effective than others, few, if any, work for all individuals in a target population. In many cases, a treatment may be extremely effective for some subset of a population, but mildly effective, ineffective, or even harmful, for others. Even if an experimental treatment is at least mildly effective for an entire population, the standard of care may still be preferred for some individuals if, for example, the experimental treatment is very expensive and there is little difference in effectiveness between the two [Song and Pepe, 2004]. Thus, it is desirable to know which individuals in a population, if any, will respond well to a particular treatment. In particular, the identification of the characteristics which lead to these individuals showing an enhanced response is of interest, as this may allow future members of the population to be assigned the treatment which will benefit them the most.
In recent years, many authors have proposed methods which use randomized clin- ical trial or observational data to obtain a set of “rules” based on patient information,
29 30
which can subsequently be used to help ensure that future individuals in the popula-
tion are assigned the treatment which is best for them [Friedman and Fisher, 1999,
Negassa et al., 2005, Gunter et al., 2007, Su et al., 2008, 2009, Brinkley et al., 2010,
Cai et al., 2011, Foster et al., 2011, Janes et al., 2011, Lipkovich et al., 2011, Qian
and Murphy, 2011, Zhao et al., 2011, Imai and Ratkovic, 2012, Zhang et al., 2012].
The resulting “rules” may vary widely in form and complexity, from simple regions of
the design space, such as x3 > 5 or {x1 > 0.5, x6 < 1}, to more complex inequalities,
such as f(x) > c, where c is some constant and f is some nontrivial p-to-1 function of the covariate vector x.
In this paper, we limit our discussion to cases where the outcome is continuous, and only two treatment options are available. We are interested in cases where p, the number of baseline covariates, is moderate, e.g. 5 to 100. We consider the use of ran- domized clinical trial (RCT) data to select a simple treatment “regime” [Zhang et al.,
2012] which, if followed by the entire population, leads to the best expected outcome.
Potential regimes are restricted to those which involve assigning one treatment to individuals who are in a region, say A, of the covariate space, and assigning the other treatment to those individuals in Ac. It is desirable that these regions be simple, and depend on only a limited number of covariates, so potential regions are limited to contiguous subsets of the covariate space defined by one, two and three variables, such as {x1 > 0, x2 > 0} or {x3 < 5, x4 > 0, x7 < 1}. These simple regions are easy
to understand, and allow for future treatment decisions to potentially be faster, less
expensive or less invasive, as they require only a limited amount of necessary patient
information. In addition to providing a “nice” functional form, limiting the number
of covariates that define the regions allows one to potentially identify the covariates
which most strongly affect how a patient will respond to treatment. 31
The remainder of this chapter is as follows. In Section 2 we describe the proposed
method and outline an algorithm for implementation. In Section 3 we present the
results of a simulation study, and in Section 4, we discuss the application of the
proposed methods to a prehypertension RCT data set.
3.2 Identifying subgroups using the average value function
Suppose we have independent observations (y1, x1),..., (yn, xn) from the general
model
yi = h(xi) + (Ti − π)g(xi) + i, (3.1)
where y is a continuous outcome, g and h are unknown functions, T is a binary
treatment indicator, π is the treatment randomization probability, and 1, . . . , n are
iid errors with mean zero and variance σ2. Without loss of generality, assume that
higher values of y represent an improved response. We wish to estimate a subregion,
Aˆ, of the covariate space with which to define our treatment regime. In future pop-
ulations, only individuals in region Aˆ would receive treatment (T = 1), with those
in Aˆc receiving the standard of care (T = 0). We wish to select the region Aˆ which
maximizes the expected response under this regime. This expectation is sometimes
referred to as the average Value [Sutton and Barto, 1998, Gunter et al., 2007]. Note ˆ that g(xi) is the treatment effect for subject i, so if we had no restrictions on A and
g were known, the best regime would be to treat all individuals with g(xi) ≥ 0. The
functions g(x) and h(x) may be complex, potentially involving non-linearities and interactions, so the approach we take is to use non-parametric methods to estimate g and h. These estimates are then used to select the “optimal” region Aˆ, with the
restriction that Aˆ has to be simple. 32
3.2.1 Nonparametric estimation of g and h
The following iterative approach is used to estimated the unknown functions h and g in (3.1):
(i) Fit the model y = h(x) to obtain the initial estimate of h, hˆ(1).
1 ˆ(k) th (k) (ii) Fit the model T −π (y − h (x)) = g(x) to obtain the k estimate of g,g ˆ , k ≥ 1.
(iii) Fit the model y − (T − π)ˆg(k)(x) = h(x) to obtain the (k + 1)th estimate of h,
hˆ(k+1), where k ≥ 1.
h i2 Pn ˆ(k) (k) (iv) Iterate between steps (ii) and (iii) until i=1 yi − h (xi) − (T − π)ˆg (xi) changes by less than a prespecified small number.
There are many possible choices of model or algorithm for estimating g and h in steps
(ii) and (iii), such as multivariate adaptive regression spline (MARS) [Friedman, 1991]
and Random Forests [Breiman, 2001]. One may wish to choose the “convergence
threshold” in step (iv) above differently depending on which estimation method is
chosen. For instance, in our experience, a threshold of around 10−5 can generally
be achieved within only a few iterations for methods such as MARS and generalized
additive models. For Random Forests, the amount by which the sum of squares in
step (iv) changes remains somewhat constant, regardless of how many iterations have
been performed, most likely because of the random nature of this method. Thus,
in this case, we instead continue until 60 iterations have been performed, as in our
experience this is more than enough to obtain good estimates of g(x) and h(x). 33
3.2.2 Selecting a subgroup for fixed g and h
Using notation similar to Zhang et al. [2012], let y1i and y0i be the potential responses given that subject i received treatment or the standard of care respectively,
∗ so that yi = y1iTi + y0i(1 − Ti). Let yi (A) = y1iI(xi ∈ A) + y0i(1 − I(xi ∈ A)) be the potential outcome for a future subject under this “treat-if-in-A” regime for any region A. After some simple algebra, we have
h i h i ∗ ∗ E yi (A) = E E yi (A) xi,A h i h i h i = E h(xi) − E πg(xi) + E 2πg(xi)I(xi ∈ A) . (3.2)
Note that only the last term in (3.2) involves A, so maximizing the expected value of
∗ yi (A) with respect to A amounts to maximizing
h i EX g(xi)I(xi ∈ A) . (3.3)
Thus, given function g, one estimator for (3.3) is the sample average:
n 1 X g(x )I(x ∈ A), n i i i=1
which, after multiplying by n, can be rewritten as
X g(xi). (3.4)
i:xi∈A
The chosen subgroup, Aˆ, is that which maximizes (3.4). In practice, one may wish to
consider the inclusion of a nonzero offset in (3.4), as in our experience this can help 34 to better identify truly positive responders. Specifically, one could replace (3.4) with
X [g(xi) − δ], (3.5)
i:xi∈A where δ 6= 0. Selection of the offset δ is considered below.
n ≥ o We consider one, two and three-dimensional regions of the general form xj < cj ,or n ≥ o n ≥ o n ≥ o n ≥ o n ≥ o xj < cj ∩ xk < ck or xj < cj ∩ xk < ck ∩ xl < cl as candidates for the ˆ ≥ region A, where < indicates either ≥ or < and j, k and l are distinct. In addition, we consider the complements of these regions.
Once the final converged estimates, hˆ andg ˆ, are obtained, the optimal region Aˆ can be found by replacing g withg ˆ in (3.4) or (3.5) and maximizing with respect to A. For the remainder of the paper, this subgroup identification method will be referred to as the Average Value (AV) approach.
Note that for just the three-variable candidate regions specified above, there are
p 3 3 unique combinations of covariates, 2 = 8 unique ways to assign directions ≥ / < to xj, xk and xl, and as many as n−1 unique cutpoints for each covariate (if observed values are unique). Thus, the Average Value procedure will often involve the evalu- ation of a very large number of regions, making it very computationally expensive.
Therefore, a modified version of the procecure is employed in our simulations and example data analysis. Specifically, to decrease the number of candidate groups, we consider a rough, evenly-spaced grid of 10 to 20 cutpoints, rather than all observed values as candidates for the cutpoint cj for covariate j, j = 1, . . . , p. Additionally, instead of considering all one, two and three-dimensional regions simultaneously, we employ a “stepwise” approach. This approach is as follows:
1. Evaluate all candidate one-dimensional regions, and select the best M1D re- 35
gions. Let B1D be the set of unique covariates which define these “best” one-
dimensional regions.
2. Evaluate all candidate two-dimensional regions in which one of the dimensions
is defined by a member of B1D and the other is any other covariate (that may
or may not be in B1D), and select the best M2D regions. Let B2D be the set
of unique pairs of covariates which define these “best” two-dimensional regions.
Note that B1D is only used to define which covariates are allowed to define
one of the dimensions of the two-dimensional regions. All possible directions
(i.e. < or ≥) and cutpoints are considered for these covariates when evaluating
two-dimensional regions.
3. Evaluate all candidate three-dimensional regions in which two of the dimensions
are defined by a pair contained within B2D and the other is any other covariate
(that may or may not be in B2D), and select the best three-dimensional region.
As in step 2, B2D is only used to define which covariates are allowed to define
two of the dimensions of the three-dimensional groups, so all possible directions
(i.e. < or ≥) and cutpoints are considered for these covariates when evaluating
three-dimensional regions.
4. Identify Aˆ, the best overall region.
It should be noted that, if one wishes to restrict the minimum or maximum size of candidate subgroups, this can be done by simply removing groups outside of this size range from consideration. This may also help to improve the computational efficiency of the AV method, as it further decreases the number of subgroups which must be evaluated. 36
3.2.3 Evaluation of the region Aˆ
The proposed method always identifies a region, so it is important to have a
method by which to evaluate the strength of the selected region. For this purpose,
we consider the metric proposed by Foster et al. [2011]:
Q(A) = E(y|T = 1, x ∈ A) − E(y|T = 0, x ∈ A) − [E(y|T = 1) − E(y|T = 0)], (3.6)
which is a measure of the enhanced treatment effect in A relative to the average
treatment effect. We consider six methods for estimating (3.6), which we briefly
describe below. Additional details are given by Foster et al. [2011].
Method 1. Resubstitution. Replace the four conditional expectations in (3.6)
with the observed means in the data and use these obtain an estimate of Q(A):
Pn Pn ˆ i=1 yiI(xi ∈ A, Ti = 1) i=1 yiI(xi ∈ A, Ti = 0) Q(A)RS = Pn − Pn i=1 I(xi ∈ A, Ti = 1) i=1 I(xi ∈ A, Ti = 0) "Pn Pn # i=1 yiI(Ti = 1) i=1 yiI(Ti = 0) − Pn − Pn . (3.7) i=1 I(Ti = 1) i=1 I(Ti = 0)
As noted by Foster et al. [2011], the Resubstitution method re-uses the data
which were used to estimate Aˆ. Thus, this estimate is expected to be positively
biased.
Method 2. Simulate new data. The goal of this method is to obtain new data
which “look like” the original data, but are independent of the original data,
thereby reducing the bias of the resulting estimate. This process could be re-
peated many times, and each time (3.7) could be recalculated using the new
data. The simulate new data estimate could be found by averaging these resub- 37
stitution estimates. As in Foster et al. [2011], we avoid actually simulating new ˆ data by instead replacing yi byy ˆi = h(xi) + (Ti − π)ˆg(xi), i = 1, . . . , n in (3.7). ˆ This estimate is denoted Q(A)SND. This method also tends to be positively
biased, but is generally less biased than the RS approach. It should be noted
that, though we do not actually simulate new data in this method, we use the
name “simulate new data” in order to be consistent with Foster et al. [2011].
Method 3. Mean gˆ. For a given sample, under model (3.1), the empirical version
of (3.6) is equivalent to
1 P g(x ) − 1 Pn g(x ), where |A| is the number of individuals in the |A| i:xi∈A i n i=1 i region A. Thus,g ˆ can be used to obtain an estimate of (3.1):
n 1 X 1 X Qˆ(A) = gˆ(x ) − gˆ(x ). (3.8) gˆ |A| i n i i:xi∈A i=1
This method is similar to the SND method, and will generally have a similar
amount of bias. It should be noted that for “paired” data, in which each treated
observation has a corresponding identical (with respect to covariate values)
control observation, this estimate will be exactly equal to the SND estimate.
Methods 4-6. Bootstrap bias correction. We also consider the bootstrap bias
correction discussed in [Foster et al., 2011]. For a given region A, the bias of an
estimate, Qˆ(A), of (3.6) is Qˆ(A) − Q(A). Following the arguments provided in
[Foster et al., 2011], it is possible to obtain an approximation to this bias using
bootstrap data sets. Let sample l represent a bootstrap sample taken with
replacement from the observed data. Using this sample, the Average Value
approach is implemented, providing new estimates hˆ(l),g ˆ(l) and a new region 38
A(l). A new estimate Qˆ(l)(A(l)) of (3.6) is then obtained from one of the above
methods, and can be viewed as an approximate estimate of Qˆ(A). Additionally,
the observed data and corresponding function estimates hˆ andg ˆ may be used
along with the new region A(l) to calculate Qˆ(A(l)), which can be viewed as an
approximate estimate of Q(A). Thus, a bootstrap approximation of the bias
is Qˆ(l)(A(l)) − Qˆ(A(l)). This process is repeated many times (say, L), and the
ˆ 1 PL ˆ(l) (l) ˆ (l) bias of Q(A) is approximated by L l=1(Q (A ) − Q(A )). The resulting estimate may be used to adjust estimates from any of the above three methods,
ˆ ˆ 1 PL ˆ(l) (l) ˆ (l) i.e. the adjusted Q(A) = Q(A) − L l=1(Q (A ) − Q(A )). These adjusted RS, SND andg ˆ-based estimates are called Methods 4, 5 and 6 respectively.
3.2.4 Selection of δ
If one wishes to consider an offset, δ, a number of options exist. In this paper, we use the offset to improve the performace of our method, and we select the smallest value δ such that (−δ, δ) contains at least 50% of the estimated treatment effects, gˆ(xi), i = 1, . . . , n, thus forcing the estimated subgroup to contain fewer than half of the observations. This value tends to be large, and was selected because we wish to aggressively search for enhanced individuals. It should be noted that, though we use a positive, nonzero δ, we consider anyone with a treatment effect greater than zero to be enhanced. If one instead considers “enhanced” individuals to be those beyond some known, nonzero, minimal meaningful treatment effect (say, c), one could instead define the offset to be δ + c, where δ is still nonzero. Alternatively, if one wishes for the selected subset to be of a specific size, the value of δ could be chosen accordingly.
If one wishes to be less aggressive, an offset need not be used. 39
3.3 Simulations
To evaluate the performance of the proposed method a simulation study was un- dertaken. In this study, the proposed method is compared to the Virtual Twins
[Foster et al., 2011] approach, which is another two-stage subgroup identification pro- cedure. In the first stage of the Virtual Twins procedure, y is used as the outcome in a Random Forest, with the covariates and treatment indicator being used as predic- tors. This Random Forest is used to obtain estimates of the two potential outcomes, y1i and y0i, for each subject, and the estimated treatment effecty ˆ1i − yˆ0i is calculated for each subject. In the second stage, the estimated treatment effects are used as the outcome in a single regression tree, and the identified subgroup consists of all terminal nodes for which the estimated treatment effect (from the single regression tree, not the Random Forest) is beyond some pre-defined “enhancement” threshold.
In this simulation study, we consider six different cases, as shown below:
1. g(x) = √5 (x + x ) 2 1 2 0.5 + 10 min(|x1|, |x2|) if x1 > 0.5 and x2 > 0.5 2. g(x) = −0.5 if x1 < −0.5 or x2 < −0.5 min(|x1 + 0.5|, |x2 + 0.5|) − 0.5 otherwise
3. g(x) = 20I(x1 > 0, x2 > 0) min(|x1|, |x2|)
4. g(x) = 35I(x1 > 0, x2 > 0)
5. g(x) = 5
6. g(x) = 0. 40
In all cases, at most 2 of the p variables determine g(x). In case 1, treatment effects
are generated by summing values of the first two covariates. Because the covariates
are normally distributed with mean zero, the resulting treatment effects have a distri-
bution which is symmetric about zero. Thus, there is no clearly separated “enhanced”
group of individuals who are different from the rest of the population. However, in-
dividuals with x1 + x2 > 0 show a positive expected response to treatment and those with x1 + x2 < 0 show a negative expected response to treatment. Cases 2-4 have clearly defined enhanced individuals present. In case 2, there is a group of “nonre- sponders” whose values for g vary slightly around zero, and a group of “responders”, whose values for g vary around some nonzero mean treatment effect. Case 3 is simi- lar to case 2, but nonresponders show no effect of treatment whatsoever, rather than small effects centered at zero. In case 4, nonresponders again have a constant zero treatment effect, and responders have a constant nonzero treatment effect. Cases 5 and 6 are two variants on a null case. In case 5, the treatment effect is a non-zero constant for all individuals, so no “enhanced” region exists, or alternatively, everyone is “enhanced.” In case 6, the treatment effect is exactly zero for all members of the population. Specific data generation schemes for all six cases are given below. For each case, 100 data sets of size n = 500 were generated from the model:
yi = 30 + 5x1i + 5x2i − 5x7i + Tig(xi) + i, where x’s are iid standard normal, ’s are iid normal with mean zero and variance
100 and are independent of the x’s. In all cases, we consider a total of 10 variables (8 of which may be considered “noise” variables) in our analysis. For cases 1-4, three- dimensional plots of x1, x2 and g are given in Figure 3.1 and histograms of g from all 41
100 data sets can be found in Figure 3.2. The “true” enhanced region in each case
1 consists of all individuals for whom g(xi) > 0. Thus, in case 1 we expect 2 of the
1 subjects to be enhanced, in cases 2-4 we expect 4 of the population to be enhanced, in case 5 the true region is all individuals, and in case 6 the true region is empty.
For the Average Value approach, only subgroups of size 20 or larger were consid- ered. It should be noted that this value is somewhat arbitrary. Additionally, for the stepwise subgroup search, the top 10 (M1D = 10) of the one-dimensional regions were used to identify covariates for B1D and the top five of the two-dimensional groups of c n ≥ ≥ o n ≥ ≥ o the form xi < ci, xj < cj (and top five groups of the form xi < ci, xj < cj ) were used to identify covariate pairs for B2D (when combined, gives M2D = 10). Candi- date cutpoints for each covariate were the corresponding 0, 5, 7.5,..., 95 percentiles for the one-dimensional search, 0, 5, 10,..., 95 percentiles for the two-dimensional search and 0, 5, 20, 35, 50, 65, 80, 95 percentiles for the three-dimensional search. It should be noted that the 0th quantiles were included as candidate cutpoints to allow for the identification of subgroups of less than three variables, since ≥ 0th percentile means the corresponding variable is useless. For both the Average Value and Virtual Twins procedures, 20 bootstrap data sets were used to obtain the bias-corrected estimates.
As mentioned above, for the Average Value procedure, we selected an offset δ such that (−δ, δ) contains at least 50% of the estimated treatment effects. This offset value was also used as the “enhancement” threshold for the Virtual Twins procedure. For the Average Value procedure, the unknown functions g and h were estimated using a simple average MARS estimates and Random Forest estimates, as this approach was found to perform better than either method alone in our simulations. These estimates were obtained using the R functions randomForest and mars with default settings.
For each case, to assess the ability of the methods to identify the true underlying 42 subgroup, we calculate the average number of individuals with a true positive treat- ment effect, the average size of the identified region, the average sensitivity, specificity, positive and negative predictive values for the identified regions, the proportion of the time in which the correct covariates are included in the identified regions, and the proportion of the times the identified subgroup is defined using only the correct co- variates. In addition, for each case we calculate the average values of Q(A), Q(Aˆ) and all the estimates of Q(Aˆ) discussed in Section 2.2.3. In the calculation of sensitivity, specificity, positive predictive value and negative predictive value, we consider the
“true” region to be all individuals for whom g(xi) > 0 and the “estimated” region to be all individuals in Aˆ.
Table 3.1, shows that the Average Value approach tends to identify larger sub- groups than Virtual Twins, especially when there exists a subgroup of patients with especially large treatment effects, such as in Cases 3 and 4. Because of this, the
Average Value approach tends to have slightly better sensitivity and slightly lower positive predictive value than Virtual Twins. This tendency to select larger groups also leads to slightly lower specificity for the Average Value approach compared to
Virtual Twins, especially when some very enhanced individuals exist (Cases 3 and
4), as the Average Value approach tends to identify too many individuals as being enhanced in these cases. Both methods tend to identify too few individuals as being enhanced in situations where there are many individuals with small to moderate treat- ment effects, such as in Cases 1, 2 and 5; however, this is to be expected, as a large offset was selected in order to aggressively search for very enhanced individuals. The
Average Value method is generally very successful at identifying regions which de- pend on the true important covariates, and this success appears to be less sensitive to changes in scenario than that of the Virtual Twins approach. The Virtual Twins ap- 43 proach more frequently identifies regions which depend only on the correct covariates.
Both of these trends are most likely a result of the Average Value method’s tendency to select three-dimensional regions, regardless of the true underlying dimension.
From Table 3.2, we can see that the Virtual Twins procedure tends to identify more enhanced regions than the Average Value procedure. This is most likely due to the fact that Virtual Twins tends to identify fewer subjects as being enhanced than the Average Value procedure. The uncorrected estimates of Q(Aˆ) tend to be less biased for Virtual Twins than for the Average Value procedure, most likely because the Average Value procedure selects less enhanced regions, and as noted by Foster et al. [2011], these estimates tend to be more biased when Q(Aˆ) is small (or zero). As expected, the uncorrected SND estimates are less biased than the RS estimates for both procedures. Also, for the Average Value approach, the Meang ˆ estimate appears to be a slight improvement over the SND estimate. The bias correction appears to work better for the Average Value method, showing less of a tendency to overcorrect than with Virtual Twins, perhaps because the estimates of Q(Aˆ) tend to be more biased for the Average Value procedure than for Virtual Twins.
It is difficult to identify one estimate as the best performer for all cases for either method. For non-null cases (1-4), the uncorrected SND estimates appear to be best for Virtual Twins, while the bias-corrected RS estimates generally perform best for the Average Value method. Though it tends to overcorrect, the bias-corrected Mean gˆ estimate also seems promising, especially for null cases 5 and 6. For the Virtual
Twins procedure, the bias-corrected RS estimates appear to be best for cases 5 and
6.
In our experience, the Virtual Twins procedure has a tendency to identify sub- groups which consist of two or more disjoint regions, whereas the Average Value 44 method is designed to identify only contiguous regions. Because of this, subgroups identified by the Average Value method will generally be simpler and easier to use than those identified by Virtual Twins. Moreover, the results of this simulation study suggest that further restricting the form of potential subgroups has only a very mild negative impact on performace (compared to Virtual Twins). Thus, we believe the
Average Value procedure is a very viable alternative to Virtual Twins.
Table 3.1: Simulation study results: subgroup identification performance
True # Incl. Only 1 Scenario Responders Size Sens. Spec. PPV NPV x1, x2 x1, x2
Case 1 AV: 249.94 98.84 0.36 0.97 0.93 0.61 0.99 0.11 VT: 249.94 95.12 0.36 0.98 0.92 0.61 0.94 0.43 Case 2 AV: 125.27 103.08 0.33 0.84 0.42 0.79 1.00 0.10 VT: 125.27 78.88 0.37 0.91 0.62 0.82 0.81 0.12 Case 3 AV: 125.27 171.37 0.69 0.77 0.53 0.89 1.00 0.21 VT: 125.27 118.79 0.62 0.89 0.73 0.88 1.00 0.43 Case 4 AV: 125.27 204.32 0.99 0.79 0.63 1.00 1.00 0.53 VT: 125.27 129.93 0.97 0.98 0.96 0.99 1.00 1.00 Case 5 AV: 500 239.30 0.48 - 1.00 - - - VT: 500 231.64 0.46 - 1.00 - - - Case 6 AV: 0 76.74 - 0.85 - 1.00 - - VT: 0 49.42 - 0.90 - 1.00 - -
1 True responders defines as those with g(xi) > 0. AV and VT indicate Average Value and Virtual Twins respectively. Sample size for each case is 500. 45
20 30
25 10 20
g(x) g(x) 0 15
10 −10 5
−20 0 3 3 2 2 1 1 0 0 x1 x1
−1 3 −1 3 2 2 1 1 −2 0 −2 0 −1 −1 x2 x2 −3 −2 −3 −2 −3 −3
(a) Case 1 (b) Case 2
60
50 30
40
g(x) 20
30 g(x)
20 10 10
0 0 3 3 2 2 1 1 0 0 x1 x1
−1 3 −1 3 2 2 1 1 −2 0 −2 0 −1 −1 x2 x2 −3 −2 −3 −2 −3 −3
(c) Case 3 (d) Case 4
Figure 3.1: Plot of True g(x) for Cases 1-4
3.4 Application to randomized clinical trial data
The proposed methods were applied to data from the Trial of Preventing Hy- pertension (TROPHY) [Julius et al., 2006]. This study included participants with prehypertension, meaning that all participants had either an average systolic blood pressure of 130 to 139 mm Hg and diastolic blood pressure of no more than 89mm Hg 46 0.08 0.3 0.06 0.2 0.04 Density Density 0.1 0.02 0.0 0.00
−20 −10 0 10 20 −5 0 5 10 15 20 25
True g(x) True g(x)
(a) Case 1 (b) Case 2 0.15 0.3 0.10 0.2 Density Density 0.05 0.1 0.0 0.00
0 10 20 30 40 50 0 5 10 15 20 25 30 35
True g(x) True g(x)
(c) Case 3 (d) Case 4
Figure 3.2: Histogram of True g(x) for Cases 1-4
for the three run-in visits (before randomization), or systolic pressure of 139 mm Hg or lower and diastolic pressure between 85 and 89 mm Hg for the three run-in visits.
These subjects were randomly assigned to receive either two years of candesartan (a hypertension treatment) or placebo, followed by two years of placebo for all subjects.
Subjects had return visits at 1 and 3 months post-randomization, and every 3 months 47
Table 3.2: Simulation study results: Q(Aˆ) estimation performance
Qˆ(Aˆ) Bias-Corrected Qˆ(Aˆ) Scenario Q(A) Q(Aˆ) RS SND Meang ˆ RS SND Meang ˆ
Case 1 AV: 4.00 5.43 8.00 6.63 6.63 4.97 2.79 3.51 VT: 4.00 6.19 7.92 6.29 - 4.00 1.16 - Case 2 AV: 3.03 1.38 6.10 4.38 4.11 2.82 0.19 0.65 VT: 3.03 4.31 6.45 4.91 - 1.62 -1.16 - Case 3 AV: 7.02 3.63 5.63 4.53 4.37 3.29 1.53 1.92 VT: 7.02 7.71 9.01 7.17 - 5.51 2.67 - Case 4 AV: 26.23 13.31 14.36 11.72 11.28 13.23 9.98 10.32 VT: 26.23 24.95 25.01 23.20 - 24.28 22.20 - Case 5 AV: 0.00 0.00 2.69 1.87 1.79 0.54 -0.90 -0.61 VT: 0.00 0.38 2.49 2.20 - -1.47 -2.56 - Case 6 AV: 0.00 0.00 6.12 4.33 3.85 2.33 -0.43 -0.09 VT: 0.00 0.41 2.75 2.29 - -0.77 -2.05 -
AV and VT indicate Average Value and Virtual Twins respectively. Sample size for each case is 500. thereafter until month 24. In year 3, clinic visits were at 25 and 27 months, and then every third month thereafter until the end of the study. The study produced analyz- able data on 772 subject, with 391 coming from the candesartan group and 381 from the placebo group. Baseline measurements included age, gender, race (white, black or other), weight, body-mass index (BMI), systolic and diastolic blood pressures, to- tal cholesterol, high density lipoprotein cholesterol (HDL), low density lipoprotein cholesterol (LDL), HDL:LDL ratio, triglycerides, fasting glucose, total insulin, in- sulin:glucose ratio and creatinine, with the insulin:glucose ratio being dropped from our analysis due to extremely high correlation (≈ 0.98) with total insulin. The end- 48 point of interest in the original study was the binary variable development of stage
1 hypertension (see Julius et al. [2006] for details); however, for the purpose of this paper we consider the continuous variable systolic blood pressure as the outcome variable. Specifically, the outcome in our analysis is blood pressure (systolic) at 12 months post-randomization.
It should be noted that at 12 months post-randomization there was some (ap- proximately 20%) missing data in the outcome due to patient dropout and patients developing hypertension (the endpoint in the original study). For our analysis, be- cause the endpoint (hypertension) was defined based only on observed blood pressure measurements, missing data due to patients experiencing the event were assumed to be missing at random. There was also a small amount of missingness in the base- line covariates, with the largest fraction of missing for any covariate being 4.3%. All missing values were imputed using SAS PROC MI (SAS Institute Inc., Cary, NC).
The imputation model included all baseline covariates and all blood pressure mea- surements up to 12 months post-randomization, stratified by treatment and gender.
Because the proposed methods have not yet been extended to data with missing values, only a single imputation was perfomed.
There are three very large and influential outliers in the covariate values. Thus,
Random Forests, rather than an average of Random Forests and MARS, was used to estimate the unknown functions g and h, as it is less sensitive to outliers than
MARS. Additionally, insulin, glucose, HDL, LDL, HDL:LDL ratio and triglycerides were noticeably skewed, so these covariates were log-transformed for the analysis.
In our analysis, we used the following settings for the Average Value method: (1) the percentiles of covariates used as cutpoints in the three-dimensional search were changed to 0, 7.5, 15, . . . , 90, (2) all two-dimensional regions were considered in the 49
stepwise search procedure (so that B1D contained all the baseline covariates), (3) the
top 50 two-dimensional groups (and the top 50 complement groups) were used to
identify covariate pairs for B2D (so M2D = 100), and (4) the Random Forest included
2000 trees. All other settings were the same as those in the simulations.
A histogram of the estimated treatment effects is given in Figure 3.3. The very
high percentage of positive predicted treatment effects suggests that candesartan is
widely effective for treating prehypertension. Thus, in this case, it may be more inter-
esting to identify the small subgroup of individuals who shouldn’t receive treatment.
As a result, no offset was used in this analysis (δ = 0), and Aˆ was redefined as the region which minimizes (3.5).
The identified region is Aˆ = {HDL:LDL ratio < 0.38, HDL cholesterol < 46.02, total insulin ≥ 25.11}, and contains 20 subjects. Thus, the Average Value method suggests a treatment regime where individuals in this region receive placebo and all others receive candesartan. Estimates of Q(Aˆ) were -1.63, -8.14 and -9.75 for the RS,
SND and Meang ˆ methods respectively, with bias corrected values being 3.92, 0.35 and
-4.24. The bias corrected estimates are closer to zero than the uncorrected estimates, and are fairly small in magnitude, suggesting that individuals in the identified region may have essentially no response to treatment, rather than a large negative response.
It should be noted that, due to the random nature of Random Forests, results may vary slightly depending on which seed is chosen for the estimation of the functions g and h. The above analysis was repeated using a different random seed, and a slightly different subgroup was identified; however, the subgroup was again defined using insulin and two of the cholesterol measures, and contained some, but not all of the same individuals. The above analysis was also performed without the three large outlying observations in the covariates, and again a region based on cholesterol 50 200 150 100 Frequency 50 0
−10 0 10 20 30
Estimated Treatment Effect
Figure 3.3: Histogram ofg ˆ(x) for TROPHY Data
measures and insulin was identified. Given the relatively small magnitude of the bias- corrected estimates of Q(Aˆ), it is also possible that the selection of different covariates and subjects with different seeds is due to the fact that no “true” subgroup exists.
3.5 Discussion
We proposed a method which uses randomized clinical trial data to identify sim- ple sets of “rules” based on patient information, which can be used to define future 51 treatment regimes. The method was found to be very effective at identifying truly im- portant covariates in simulations, but had a tendency to identify larger, and therefore less enhanced subgroups than Virtual Twins [Foster et al., 2011]. Though slightly less enhanced, the subgroups identified by the Average Value procedure were generally comparable to those from Virtual Twins, and have the added advantage of being sim- pler, and therefore easier to interpret, which may lead to them seeing more real-world use.
Due to slight differences between the proposed method and Virtual Twins, it is difficult to know if the results in the simulation section are directly comparable. For instance, an offset of, say 10 for the Average Value procedure may not be equiva- lent to an “enhancement” threshold of 10 in Virtual Twins. Additionally, a direct comparision may not be fair because, as previously mentioned, the Average Value procedure does not allow the same subgroup complexity as Virtual Twins.
Though very effective at identifying truly important covariates, the proposed method tends to select three-dimensional regions, even when the true underlying region is of fewer dimensions. Thus, it may be interesting to consider some form of pruning, as is done for classification and regression trees. This would be particularly interesting if one wished to consider subgroups of more than three dimensions. Al- ternatively, it may be interesting to consider incorporating a penalty based on the number of covariates to the objective function. It is possible that the inclusion of such a penalty could help the Average Value method to more frequently identify regions of the correct dimension.
The general strategy used in this paper is to first estimate g(xi), and then find P ˆ the region A which maximizes i∈A gˆ(xi), where we restrict A to have a certain simple form. Other simple forms of Aˆ could also be considered. For example, Aˆ could 52 be defined by {x : βT x > c}, with further simplification possible if the number of non-zero βj’s was also restricted.
It should be noted that the chosen value of the offset δ can strongly impact the size of the estimated subgroup. Thus, it may be possible to improve the performance of the Average Value approach by using alternative data-adaptive methods for selecting
δ.
Because of the computationally expensive nature of the Average Value method, we considered a more computationally efficient “stepwise” version of the procedure in our data analysis and simulations. It may be of interest to consider less greedy methods for increasing the speed of the procedure. CHAPTER 4
Permutation testing for treatment-covariate interactions
4.1 Introduction
In clinical trials, a common goal is to search for subgroups of enhanced treat- ment effect. A well-known risk in subgroup analysis is that of false positives [Yusuf et al., 1991, Peto et al., 1995, Assmann et al., 2000, Brookes et al., 2001, Cui et al.,
2002, Pocock et al., 2002, Brookes et al., 2004, Rothwell, 2005, Lagakos, 2006, Wang et al., 2007]. One way to reduce this risk is to pre-define a small number of potential subgroups before looking at the data; however, one may not always know a priori which subgroups may be of interest. When considering pre-defined subgroups, one common approach to reducing the risk of false positive findings is to consider a mul- tiple testing procedure, such as a Bonferroni correction. Multiple testing procedures can effectively reduce false positives, but generally also lack power to detect true sub- groups. Thus, one may instead wish to pre-define a statistical approach for identifying subgroups [Ruberg et al., 2010], which can be implemented using the data [Friedman and Fisher, 1999, Negassa et al., 2005, Su et al., 2008, 2009, Brinkley et al., 2010,
Cai et al., 2011, Foster et al., 2011, Lipkovich et al., 2011, Qian and Murphy, 2011,
53 54
Zhao et al., 2011, Imai and Ratkovic, 2012, Zhang et al., 2012]. Such pre-defined
approaches can be very effective, but may still be prone to identifying subgroups,
even when no true underlying subgroup exists [Foster et al., 2011]. To help quantify
the potential usefulness of identified subgroups, Foster et al. [2011] considered the use
of a metric, Q(A), which is defined as the difference between the expected treatment effect in some subset of the covariate space, A, and the overall treatment effect. Such a metric can also be helpful for eliminating false subgroups, as small values suggest a lack of enhancement, but may be more effective if one can also obtain p-values for the metric estimates.
Before obtaining a p-value, one must consider what “null” means in a particular setting. Subgroups of enhanced (or more generally, different) treatment effect occur when the effect of treatment depends on the covariate values, i.e., such subgroups arise when treatment-by-covariate interactions exist. Thus, in this setting, “null” data may be defined as data in which no treatment-by-covariate interactions exist.
Alternatively, if one has implemented a subgroup identification procedure, and wishes to evaluate the identified region of the covariate space, say A, null data could be defined as data for which the treatment effect in region A is equal to the overall treatment effect. In this paper, we will focus on the more general null scenario that no treatment-by-covariate interactions exist.
Consider the following general model:
yi = h(xi) + g(xi)(Ti − π) + i, (4.1)
th where yi is the observed, continuous outcome measure for subject i, xi is the i row of the standardized, n × p covariate matrix X, and Ti is a binary indicator of which 55
treatment subject i received. Additionally, i, i = 1, . . . , n are iid errors with mean zero and variance σ2 which are independent of the covariates, and π is a treatment
randomization probability. We wish to consider a general class of models, so h and
g are unspecified. Note that in this model, g(xi) is the treatment effect at covariate
value xi. Our goal is to test the null hypothesis that g(x) is constant with respect
to the covariates x. That is, we wish to test for treatment-by-covariate interactions.
One possible approach is to develop a test statistic for which asymptotic properties can be obtained, but this may be difficult for some methods. In such cases, a common approach is to use permutation tests.
A number of authors, including Edgington [1986], Good [2000], Potthoff et al.
[2001], B˚uˇzkov´aet al. [2011] and Simon and Tibshirani [2012], have considered the testing of interactions using permutation-based methods, which work by shuffling parts of the data, such as the outcome, some or all of the covariates, or the treatment indicators, with the goal of eliminating one or more specific associations. In this chapter, we have a broad definition of what a permuted data set is. In general, permutations shuffle selected parts of the data set in such a way that the new data
“look like” the original data in some aspects, but in other aspectes, the new data differ from the original data. For example, marginal distributions are preserved, but some associations between selected variables are not preserved. Moreover, with simple permutations, it may not be possible to completely control which aspects of the original data are preserved, and which are changed. An issue which must be addressed if one wishes to test for interactions using permutation-based methods is that it is generally impossible to remove only the associations of interest by simply permuting the data [Edgington, 1986, Good, 2000, Potthoff et al., 2001, B˚uˇzkov´aet al., 2011,
Simon and Tibshirani, 2012]. One way to reduce the drawbacks of removing more than 56
just the association of interest is to “cleverly” choose a test statistic [Edgington, 1986,
Good, 2000, Potthoff et al., 2001, B˚uˇzkov´aet al., 2011], but there may not always be
an obvious choice. The “permutation-like” methods that we will develop and describe
later in this chapter have a similar characteristic of preserving some aspects of the
data structure, while not preserving other aspects, but in a somewhat more controlled
fashion. In particular, we will propose alternative forms of permutation methods,
which are designed to remove only the associations of interest, thereby avoiding some
of the potential issues with using traditional permutation tests for interactions.
The remainder of this chapter is as follows. In Section 4.2 we briefly review
permutation tests and present a variety of alternative methods for obtaining p-values.
In Section 4.3, the proposed methods are compared with a number of commonly-used
permutation-based approaches in a simulation study. In Section 4.4, the proposed
methods are implemented on real data from a randomized clinical trial, and in Section
4.5 we present a discussion.
4.2 Permutation tests
4.2.1 Review of permutation tests
Suppose we have observed data (y1, x1),..., (yn, xn), where y is some outcome and
x is a covariate of interest, and that we only consider testing the null hypothesis of
no association between y and x. This is generally done by calculating a test statistic,
say TSc , and then obtaining a p-value based on the null distribution of TSc . In lieu of
using asymptotics to determine the null distribution of TSc , one may wish to employ a
permutation test. For testing the null hypothesis that no association exists between x and y, approximately “null” data can be obtained by permuting either x or y. This is 57
essentially the same as replacing the permuted covariate with a randomly generated
noise covariate of the same distribution. Permutation tests work by repeating the
process many times (say K), each time calculating a new value of the test statistic,
(k) TSc . These K values are then used to define an approximated null distribution for
TSc , from which a p-value can be obtained.
As noted by Edgington [1986], there are two basic methods of permuting data.
One approach is the systematic [Edgington, 1986] method, in which all possible per-
mutations are considered; however, in this case, K = n! (if the observed values are unique), so for even moderate sample sizes, the number of possible permutations will be very large. An alternative approach is random [Edgington, 1986] or Monte Carlo permutation, in which only a random subset of the possible permutations are consid- ered, making it much more feasible for moderate-to-large data sets. In this paper, we consider only random permutation tests.
In the next subsection, we consider several methods which are permutation based, but are specifically designed to test only for interactions, which is something tradi- tional permutation tests are generally unable to do. Though the proposed methods could be applied to any interaction, we will limit our discussion to treatment-by- covariate interactions.
4.2.2 Modified permutation methods
Permutation tests may not be ideal if one wishes to test for interactions, as they will generally be unable to remove only the association of interest. To bet- ter understand why this is, consider the following example. Suppose we have RCT data (yi,Ti, xi), i = 1, . . . , n, and that we wish to fit the interaction model yi =
T T β0 + β xi + γ(Ti − π) + θ xi(Ti − π) + i, where β and θ are p × 1. In particular, 58
suppose we wish to test for an interaction between treatment and one covariate, say
xj. That is, we wish to test the null hypothesis θj = 0. Permuting y will eliminate
the desired interaction, but will also eliminate all main effects of the covariates and
0 the treatment, thereby making the “true” underlying model yi = β0 + i. Similarly, permuting the covariate xj or the treatment indicator T will eliminate the interac- tion, but also the corresponding main effect for either xj or T , leading to a “true” underlying model where βj = θj = 0 or γ = 0, θ = 0 respectively.
One simple way to address this issue is considered by Potthoff et al. [2001], and involves permuting the covariates of interest within levels of T . Thus, in this case, one
would permute values of xj separately for those with Ti = 1 and those with Ti = 0.
This approach will avoid removing the main effect for treatment, but still eliminates
the main effect for xj, so that the null model has βj = θj = 0. Note that if one wishes to test for all x-by-T interactions (null hypothesis θ = 0), this approach is equivalent to permuting y within levels of T .
Consider now the general model (4.1), and suppose we are interested in testing whether or not the treatment effect, g(xi), is constant with respect to the covariates ˆ xi. Additionally, suppose that model (4.1) has been fit, giving function estimates h andg ˆ, and let TSc be the sample value of the test statistic of interest. Our methods
∗ are designed to perturb the values ofg ˆ(xi) to obtain a new treatment effect, gi , which does not depend on the covariates, and which will be discussed later. Using this null treatment effect, along with the specific form of model (4.1), we obtain p-values as follows:
∗(k) ˆ ∗ (k) 1. Create a new “null” outcome, yi = h(xi)+gi (Ti −π)+˜ei , i = 1, . . . , n, where
(k) (k) e˜1 ,..., e˜n are randomly sampled (without replacement) centered residuals 59
from fitted model (4.1).
2. Using y∗(k), X and T , refit model (4.1), and obtain a new value of the test
(k) statistic, TSc .
3. Repeat steps 1 and 2 K times (i.e. k = 1,...,K), giving K values of the test
statistic, and use these values to obtain an approximate null distribution for
the test statistic.
4. Use this approximate null distribution and the test statistic value from the
observed data, TSc , to obtain a p-value (either one or two-sided).
We now consider methods which use the estimated treatment effect,g ˆ, to obtain the null treatment effect, g∗.
Mean of estimated treatment effect:
Fixed g∗ approach. Perhaps the simplest null scenario in this setting is that
of a constant treatment effect for all individuals. Thus, one natural choice
is to create null data by giving all individuals the average estimated treat-
∗ 1 Pn ¯ ment effect, so that gi = n i=1 gˆ(xi) ≡ gˆ, i = 1, . . . , n. For the remainder of this paper, this will be referred to as the fixed g∗ approach.
Fixed g∗ (RN) approach. One could also consider a variation of the fixed
g∗ case, in which individuals have treatment effects which vary randomly
around a fixed, population-wide mean. In this case, we define the null
∗ ¯ treatment effect for subject i to be gi = gˆ + ˜g,i, where ˜g is a random
permutation of the non-centered residuals gˆ − gˆ¯. This will be refered to as
the fixed g∗ random noise, or fixed g∗ (RN) approach. 60
Fixed g∗ (BN) approach. Alternatively, if one has reason to believe these
residuals do not vary equally about gˆ¯ for all subjects, one may instead
∗ ∗ ¯ consider gi = gi,Bern = gˆ + g,Bern,i, where ¯ gˆi − gˆ when a = 1 g,Bern,i = , ¯ gˆ − gˆi when a = 0 1 and a is an independently generated Bernoulli( 2 ) random variable. This will be referred to as the fixed g∗ Bernoulli noise, or fixed g∗ (BN) approach.
Randomly shuffled estimated treatment effect:
Random g∗ approach. As an alternative to the fixed treatment effect case,
one may wish to consider a scenario in which each subject’s response to
treatment is random, but does not depend on the covariates. Therefore, we
could also consider creating null data by giving each individual a random
∗ estimated treatment effect, so that gi =g ˜i, where g˜ is a random permua-
tion of the estimated treatment effects. Note that this method is actually
identical to the fixed g∗ (RN) approach. Thus, we will not consider them
separately.
Random g∗ (RN) approach. As with the fixed g∗ approach, one could also
consider the addition of random noise to the random treatment effects, g˜.
This could be done by following an approach similar to that used in the
∗ ∗ fixed g method. Specifically, we may consider gi =g ˜i + ˜g,i, where ˜g is
as defined above. This will be referred to as the random g∗ random noise,
or random g∗ (RN) approach.
∗ ∗ ∗ Random g (BN) approach. Alternatively, we may consider gi =g ˜i,Bern,
∗ ∗ where g˜Bern is a random permutation of gBern (defined above). This will be 61
referred to as the random g∗ Bernoulli noise, or random g∗ (BN) approach.
Constrained least-squares approach. One may also consider obtaining null data
by modifying the estimated treatment effects so that they are approximately
null, but with similar values to the original estimates. To do this, we use least
∗ squares to calculate a new treatment effect, gi , which is close tog ˆ(xi), but has
marginal sample correlations of zero with all the covariates. That is, we choose
∗ values gi , i = 1, . . . , n which minimize
n X ∗ 2 {gˆ(xi) − gi } i=1
∗ under the constraint that the sample correlations between g and xj, j =
1, . . . , p, are zero, or equivalently by minimizing
n p n X ∗ 2 X X ∗ {gˆ(xi) − gi } + λj gi xij i=1 j=1 i=1
∗ with respect to g , where λj, j = 1, . . . , p, are Lagrange multipliers. Note that
Pp Pn ∗ if the covariates are not centered, the penalty term becomes j=1 λj i=1(gi −
∗ g¯ )(xij − x¯j). It is straightforward to show that
1 g∗ = gˆ − Xλ, (4.2) 2 where λ = 2(XT X)−1XT gˆ.
This method will be referred to as the Lagrange g∗ approach. It should be noted
that a correlation of zero between the treatment effect and a covariate does not
necessarily mean the treatment effect is independent of the covariate. Though 62
we don’t discuss it here, one could also consider additional constraints, such as
∗ 2 ∗ ˆ g being uncorrelated with xj , or g being uncorrelated with h.
To better understand why the Lagrange method should work, note that g∗ is
T exactly equal to the residuals from the modelg ˆ(xi) = xi ω + i. Thus, the
Lagrange method works by estimating the contribution of the covariates to
the treatment effect, and then removing this estimated contribution, so that
only that part of the estimated treatment effect which does not depend on the
covariates remains.
4.3 Simulations
To evaluate the performance of the proposed methods under a variety of scenar- ios, a simulation study was performed. In addition to the proposed methods, we considered four permutation-based methods:
• Permutation of y;
• Permutation of X;
• Permutation of T ;
• Permutation of y within levels of T .
These approaches will be referred to as the permute y, permute X, permute T and permute y (in T ) methods respectively. We begin by considering a linear model with treatment-by-covariate interactions, which allows us to compare the proposed methods to both permutation and exact p-values. We then discuss simulation results for a more complex model. 63
4.3.1 Simple linear model example
Data were generated from the model
1 1 y = 3 + β x + x + x + γ T − + θ T − x + x + , 1 3 5 2 2 1 2
where ’s and all x’s are iid standard normal, and the design matrix, X, has five
columns. In this case, the test of interest (for the assumed model, given below) is
that θj = 0, j = 1,..., 5. This is a situation where the F statistic has a known
distribution, and thus an exact test exists. We considered four scenarios:
(1) θ = 0.35, γ = 0.25, β = 0.5;
(2) θ = 0, γ = 0.25, β = 0.5;
(3) θ = 0.35, γ = 0.5, β = 0.25;
(4) θ = 0, γ = 0.5, β = 0.25.
In scenarios (1) and (2), the main effects for the covariates are large, and in scenarios
(3) and (4) the main effect for treatment is large. These cases were chosen to illustrate
the potential shortcomings of traditional permutation-based tests when large main
effects exist. In each scenario, 500 data sets of size 200 were generated, and the model
T 1 T 1 y = α+β x+γ(T − 2 )+θ x(T − 2 )+ was fit, where β and θ, are 5×1 vectors. The null hypothesis was that no x-by-T interactions exist (vs. alternative that at least
one exists). To assess the sensitivity of the methods to the choice of test statistic, we
P ˆ2 computed the permutation p-values using an F statistic and also the statistic θj .
For all non-asymptotic methods, 1000 permutations were used (so K = 1000). 64
Note that, in this case, the covariates are independent, as are the observations, and
the design matrix is standardized. As a result, it can be shown that X(XT X)−1XT is
p approximately equal to ( n )I, where I is an n×n identity matrix. For the fitted model, the estimated treatment effect vector gˆ is equal to γˆ + Xθˆ, where γˆ = (ˆγ, . . . , γˆ)T .
Thus for the Lagrange method, from (4.2) we have
g∗ = gˆ − X(XT X)−1XT gˆ
= γˆ + Xθˆ − X(XT X)−1XT γˆ − X(XT X)−1XT Xθˆ
= γˆ + Xθˆ − X(XT X)−1XT γˆ − Xθˆ
= (I − X(XT X)−1XT )γˆ p ≈ 1 − γˆ ≈ γˆ, n where the last approximation is a result of the fact that, in this case, p is considerably
p ∗ smaller than n, so that n is nearly zero. In addition, for the fixed g method, we have
1 X 1 X X g∗ = (ˆγ + xT θˆ) =γ ˆ + θˆ x =γ, ˆ i n i n j ij i j i
again because covariates are standardized, so that the second term is exactly zero.
Therefore, for this specific example, the Lagrange and fixed g∗ methods are nearly
identical. Note that if the covariates were correlated, the off-diagonal elements of
X(XT X)−1XT would be non-zero, leading to unique Lagrange g∗ values for each
subject. Thus, in this case the Lagrange and Fixed g∗ methods would be different.
Looking at Figure 4.1, we can see that rejection rates when using the F statistic are generally quite similar for all methods in all four scenarios, whereas the rejection
P ˆ2 P ˆ2 rates for the statistic θj vary noticeably between methods. In particular, the θj 65
rejection rates for the permute X, permute y and permute y (in T ) methods tend to be
considerably lower than those for the other methods. This is due to the fact that these
methods remove several main effects (in addition to the desired interactions) in the
process of creating new “null” outcome values, which subsequently have larger error
P ˆ2 variances than the observed outcome values. Because θj comes from the parameter
estimates for a linear regression model, its variance depends on the variance of the
outcome values, and in particular will increase or decrease as the error variance of the
outcome increases or decreases. Thus, the permute X, permute y and permute y (in
P ˆ2 T ) methods induce “null” distributions for θj which have much larger variances
than the correct null distribution (where only the interactions are removed), leading
to larger p-values and fewer rejections. A similar effect can be seen in the permute
T method, but to a lesser degree, as this method only removes one main effect. In
contrast, the Lagrange and Fixed g∗ methods create “null” outcome values whose
variances are slightly smaller than that of the observed outcome values, causing these
methods to give elevated rejection rates. This general phenomenon is mentioned by
B˚uˇzkov´aet al. [2011], who note that permutation-based methods perform better for
statistics with a pivotal null distribution.
Overall, the best methods (not based on the exact F distribution) are fixed g∗
(BN) and fixed g∗ (RN), which have rejection rates that are nearly identical for both
P ˆ2 the F statistic and θj , and which are very close to 0.05 in the “null” scenarios (2 and 4). The random g∗ (BN) and random g∗ (RN) methods are also fairly good, but
P ˆ2 have slightly lower rejection rates for θj , again due to an elevated outcome error variance (from adding “noise” twice). Figures 4.2-4.5 further illustrate the effect of creating “null” data which has an outcome error variance that is too large (or too small). This is again most noticeably for the permute X, permute y and permute y 66
(in T ), methods, whose histograms have heavier right tails for scenarios 1 and 3 and are obviously non-uniform in scenarios 2 and 4.
P ˆ2 The results for the statistic θj help illustrate the importance of an appropriately chosen permutation method when the test statistic is somewhat ad hoc, as may be the case in situations where asymptotics are difficult to obtain.
F Statistic F Statistic 0.08 ^ 2 ^ 2 ∑ θj ∑ θj 0.8 0.06 0.6 0.04 0.4 0.02 0.2 0.0 0.00
Exact Exact Fixed g* Fixed g* LagrangePermute YPermute XPermute T LagrangePermute YPermute XPermute T Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T) Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T) (a) Scenario 1 (β = 0.5, γ = 0.25, θ = 0.35) (b) Scenario 2 (β = 0.5, γ = 0.25, θ = 0)
F Statistic F Statistic 0.08 ^ 2 ^ 2 ∑ θj ∑ θj 0.8 0.06 0.6 0.04 0.4 0.02 0.2 0.0 0.00
Exact Exact Fixed g* Fixed g* LagrangePermute YPermute XPermute T LagrangePermute YPermute XPermute T Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T) Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T) (c) Scenario 3 (β = 0.25, γ = 0.5, θ = 0.35) (d) Scenario 4 (β = 0.25, γ = 0.5, θ = 0)
Figure 4.1: Rejection rates (α = 0.05) for simple linear model simulations 67
4.3.2 Complex model example
As mentioned in the Introduction, the proposed methods were motivated by our
interest in subgroup analysis. Thus, we also considered p-values for the metric Q(Aˆ) for subgroups identified using the Average Value approach proposed in Chapter 2. As noted by Foster et al. [2011], Q(Aˆ) can be viewed as the treatment effect enhancement in the region Aˆ beyond the overall treatment effect. In this case, we are interested in testing whether or not the identified subgroup is “real,” so the null hypothesis is that Q(Aˆ) is 0 (vs. alternative that Q(Aˆ) > 0). We considered four scenarios for the true treatment effect, g:
(1) g(x) = 15I(x1 > 0, x2 > 0);
(2) g(x) = 5 (case 5 from Chapter 2);
2 (3) g(xi) = 5 + ei, i = 1, . . . , n, where ei’s are iid N(0,5 );
(4) g(x) = 0 (case 6 from Chapter 2).
Other than the treatment effect, the data generation model was identical to that in the Chapter 2 simulations. That is, data were generated from the model yi =
30 + 5x1i + 5x2i − 5x7i + Tig(xi) + i, where x’s are iid standard normal and ’s are iid normal with mean zero and variance 100 and are independent of the x’s. Scenario 1 is a modified version of case 1 from Chapter 2, with the coefficient of g reduced from
35 to 15 to reduce the power to detect a positive Q(Aˆ) (which is near 0.9 when a coefficient of 35 is used). Scenario 3 can be viewed as a more challenging “null” case, where a main effect for treatment exists, but varies randomly around a population mean, so that some subjects do have an enhanced treatment effect, but enhancement is independent of the covariates. Alternatively, scenario 3 can be viewed as being like 68 scenario 2, but with a larger error variance. For each scenario, 200 data sets of size
500 were generated. ˆ ˆ ˆ ˆ We consider the null distributions of three statistics, Q(A)RS, Q(A)SND and ˆ ˆ ˆ Q(A)gˆ, which are estimates of the enhancement metric Q(A). The first statistic,
P y T ˆ ˆ i i i Q(A)RS, is obtained by subtracting the observed marginal treatment effect, P − i Ti P i yi(1−Ti) P , from the observed treatment effect in the region Aˆ, i(1−Ti) P ˆ P ˆ i yiTiI(xi∈A) i yi(1−Ti)I(xi∈A) P ˆ − P ˆ . This is expected to be positively biased, as the same i TiI(xi∈A) i(1−Ti)I(xi∈A) data which were used to identify the region Aˆ are being used to estimate Q(Aˆ). Note that independent outcome values from approximately the same distribution could be obtained by adding random residuals to the outcome estimates, yˆ. Thus, one ˆ ˆ way to reduce the bias of Q(A)RS is to obtain independent outcome measures as ˆ ˆ described above, and use these instead of yi’s to compute Q(A)RS. This could be repeated several times, and the resulting estimates could be averaged to obtain a less biased estimate of Q(Aˆ); however, because the residuals have mean zero, this is ˆ ˆ approximately equivalent to just replacing the observed y values withy ˆs in Q(A)RS. ˆ ˆ ˆ ˆ Therefore, the second statistic, Q(A)SND, is obtained by computing Q(A)RS, but with yis replaced byy ˆis. Because the Average Value method involves directly estimating the treatment effect, Q(Aˆ) can also be estimated directly from these treatment effect
P ˆ P i gˆ(xi)I(xi∈A) i gˆ(xi) estimates, gˆ, by computing the difference P ˆ − n . This is the third i I(xi∈A) ˆ ˆ ˆ ˆ statistic, and is referred to as Q(A)gˆ, and is very similar to Q(A)SND, with the two statistics being exactly equal in the case of paired data. To obtain p-values for these statistics, we again follow the procedure outlined in subsection 3.2.2. In this case, the Average Value procedure is re-implemented each time step 2 is performed, and new values of these three test statistics are calcuated. Because the Average Value approach is computationally expensive, p-values were computed using only 100 per- 69 mutations (so K = 100). It is worth noting that the Average Value method involves nonparametric regression, and in this case we do not have an obvious test statistic, such as the F statistic in the simple linear model case, which has a known exact or asymptotic distribution for the fitted model (4.1). ˆ ˆ From Figure 4.6, we can see that the statistic Q(A)gˆ performs the best overall, showing generally high power for scenario 1, while also tending to be the closest to the desired type-I error rate of 0.05 (and rarely exceeding it) in the three null cases. The ˆ ˆ ˆ ˆ statistics Q(A)RS and Q(A)SND perform well for the permute X and permute y (in
T ) approaches in scenario 1, but nearly always noticeably exceed the desired type-I error level in the three null cases. The very high type-I errors for the RS and SND estimates observed in scenarios 2 and 3 for the permute y and permute T methods are most likely due to instability in these metrics when the identified region Aˆ is extremely small, as is often the case for the “null” data sets created by permuting y or permuting T .
Histograms of p-values for the four complex scenarios for all three metrics are given in Figures 4.7 - 4.10. For scenario 1 (Figure 4.7), the histograms generally have the desired “right-skewed” shape, with the exception of the permute y and permute
T methods. For the null scenarios (Figures 4.8 - 4.10), we can see that histograms for the proposed methods are generally closer to uniform than those for the four simple ˆ ˆ permutation methods, especially for the statistic Q(A)gˆ. For the permute y and permute T methods, we frequently see a bimodal shape, which is again most likely a result of identifying very small regions Aˆ for “null” data created by permuting y or T .
Though they showed generally good power and type-I error, we can see that p-values for the permute X and permute y (in T ) methods are often noticeably non-uniform. 70
In general, the proposed methods perform very well, though the Lagrange method had slightly lower power in scenario 1 and generally much lower type-I errors in scenarios 2-4. The permute X and permute y (in T ) methods also performed well in the four scenarios we considered, though we suspect the performance of these two methods would suffer more in non-null scenarios where g is more complex. Based on the results from the simple and complex model simulations, it appears that the fixed g∗ and random g∗ (and their variants with Bernoulli or random noise) are the best choice. Additionally, the results of the simulation study suggest that, if one wishes to obtain p-values for the metric Q(Aˆ) for subgroups identified using the Average Value ˆ ˆ method, the best choice in test statistic is Q(A)gˆ. ˆ ˆ ˆ ˆ As noted previously, the estimates Q(A)gˆ and Q(A)SND are quite similar, and in the case of paired data, identical. Thus, the noticeably performance differences between these two methods in our simulation study were surprising. We believe that these differences are a result of identifying subgroups which do not have a similar number of treated and control subjects. In particular, when very small subgroups are identified, these differences can be quite severe, and lead to very pronounced differences between the two estimates.
4.4 Application to data from a randomized clinical trial
Recall that in Chapter 2, the Average Value method procedure was applied to pre-hypertension data from the TROPHY study [Julius et al., 2006] in an attempt to identify the subset of individuals who should not receive candesartan, a treatment for hypertension. In this analysis, the identified region was Aˆ = {HDL:LDL ratio <
0.38, HDL cholesterol < 46.02, total insulin ≥ 25.11}, contained 20 subjects, and 71
had corresponding (uncorrected) estimates of Q(Aˆ) of -1.63, -8.14 and -9.75 for the
RS, SND and Meang ˆ methods respectively. To further assess the identified subgroup, the proposed methods and the four simple permutation methods were used to obtain p-values for these uncorrected estimates. Because the Average Value approach is computationally expensive, and because a finer grid of cutpoints was considered for the TROPHY data, further decreasing the computational speed of the method, p- values were computed using 100 permutations (so K = 100).
Table 4.1: P-values for TROPHY data
Q(Aˆ) Estimate Method RS SND Meang ˆ
Fixed g∗ 0.94 0.33 0.11 Fixed g∗ (RN) 0.92 0.34 0.12 Fixed g∗ (BN) 0.95 0.34 0.12 Random g∗ (RN) 0.90 0.42 0.16 Random g∗ (BN) 0.92 0.29 0.14 Lagrange 0.94 0.37 0.17 Permute y 0.46 0.00 0.00 Permute X 0.96 0.25 0.08 Permute T 0.41 0.00 0.00 Permute y (in T ) 0.90 0.21 0.04
P-values for these three estimates for the five proposed methods and the four
simple permutation methods are given in Table 4.1. As might be expected, given
the relative magnitudes of the three estimates, the Meang ˆ statistic has the smallest
p-value for all the methods considered, followed by the SND estimate, with the RS
estimate having the largest p-values. Though somewhat large for the RS and SND
statistics, the p-values for the Meang ˆ were relatively small for the fixed g∗ (RN) and
fixed g∗ (BN) approaches (which were shown to perform the best in our simulations).
Thus, it is possible that a small subgroup of people who shouldn’t receive candesartan 72 exists, but can’t be fully demonstrated with the current data.
When we permute y or T , the new treatment effect estimates are generally centered around zero, which in this case will most likely lead to a larger “don’t treat” region than that identified using the observed data, for which nearly all treatment effect estimates were positive. These larger “don’t treat” regions for the permuted data will generally have smaller corresponding estimates of Q(Aˆ), which may be why the permute y and permute T approaches give the smallest p-values. Given the poor performance of the permute y and permute T approaches in our simulations, it may not be wise to trust these methods when testing for interactions, particularly when a somewhat ad hoc test statistic is being used.
4.5 Discussion
We proposed several permutation-based methods which can be used as an al- ternative to simple permutation test when one wishes to test for interactions. The proposed methods were shown to generally outperform simple permutation tests, particularly when we considered more complex scenarios and test statistics. These methods may help to reduce false positive findings when a pre-defined subgroup iden- tification strategy such as Virtual Twins [Foster et al., 2011] or the Average Value procedure is employed.
In the example data analysis in this paper, we considered only the estimates ˆ ˆ ˆ ˆ ˆ ˆ Q(A)RS, Q(A)SND and Q(A)gˆ as test statistics for the Average Value procedure. In the future, it may be interesting to consider the performance of the proposed methods when alternative test statistics are used. One such alternative is the Z statistic for the ˆ ˆ test of interaction (α3 = 0) in the model y = α0+α1T +α2I(x ∈ A)+α3TI(x ∈ A)+e, 73
which could be fit after the region Aˆ has been identified.
We show in the simple linear model simulations that the fixed g∗ and Lagrange
methods are slightly anti-conservative, and hypothesized that this may be due to the
∗ decreased total variance of yi compared to yi. Thus, for these methods, it may be
helpful to consider inflating the variance of the residuals in step 1 of our algorithm, so
∗ ∗ that the variance of yi matches that of yi. Similarly, the random g (RN) and random g∗ (BN) methods were overly conservative in our simple linear model simulations,
∗ which we believe is due to an increased total variance of yi relative to yi, so for these methods it may be helpful to consider deflating the variance of the residuals in step
1 of our algorithm.
We consider only a limited number of scenarios in our simulation study. Thus, in the future it may also be useful to consider a wider variety of simulation settings.
Given our example randomized clinical trial data, it may be of interest to consider a scenario in which the treatment effects are mostly positive, so that our goal is to identify the small subset of patients who should not receive treatment. In this case, we could again consider setting the offset, δ, at zero. This may help us to better understand the results in our example data analysis. Additionally, it may be interesting to assess the performance of our methods for non-null cases in which the treatment effect is more complex, so that the form of potential subgroups considered in our search does not match the underlying truth.
It may be possible to improve the performance of the various permutation meth- ods by considering a number of refinements. For example, in the first step of our algorithm, we resample residuals from the fit of model 4.1 without replacement, but we could also consider resampling these residuals with replacement. 74
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 300 300 300 300 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 300 300 300 300 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) Exact 300 300 300 Frequency Frequency Frequency 100 100 100 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value
(a) F Test
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 300 300 300 300 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 200 300 300 300 200 100 Frequency Frequency Frequency Frequency 100 50 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) 300 150 Frequency Frequency 50 100 0 0
0.0 0.4 0.8 0.0 0.4 0.8
p value p value
P ˆ2 (b) θj Figure 4.2: Histograms of p-values for simple linear scenario 1 (β = 0.5, γ = 0.25, θ = 0.35) 75
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 60 60 60 40 40 40 40 20 20 20 20 Frequency Frequency Frequency Frequency 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 60 60 60 60 40 40 40 40 20 20 20 20 Frequency Frequency Frequency Frequency 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) Exact 60 60 60 40 40 40 20 20 20 Frequency Frequency Frequency 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value
(a) F Test
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 80 60 60 60 60 40 40 40 40 20 20 Frequency Frequency Frequency Frequency 20 20 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 80 80 60 120 60 60 40 80 40 40 Frequency Frequency Frequency Frequency 20 40 20 20 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) 60 120 40 80 20 Frequency Frequency 40 0 0
0.0 0.4 0.8 0.0 0.4 0.8
p value p value
P ˆ2 (b) θj Figure 4.3: Histograms of p-values for simple linear scenario 2 (β = 0.5, γ = 0.25, θ = 0) 76
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 300 300 300 300 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 300 300 300 300 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) Exact 300 300 300 Frequency Frequency Frequency 100 100 100 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value
(a) F Test
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 300 300 300 300 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 300 300 300 300 200 Frequency Frequency Frequency Frequency 100 100 100 100 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) 300 300 200 Frequency Frequency 100 100 0 0
0.0 0.4 0.8 0.0 0.4 0.8
p value p value
P ˆ2 (b) θj Figure 4.4: Histograms of p-values for simple linear scenario 3 (β = 0.25, γ = 0.5, θ = 0.35) 77
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 60 60 60 40 40 40 40 20 20 20 20 Frequency Frequency Frequency Frequency 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 60 60 60 60 40 40 40 40 20 20 20 20 Frequency Frequency Frequency Frequency 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) Exact 60 60 60 40 40 40 20 20 20 Frequency Frequency Frequency 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value
(a) F Test
Fixed g* Fixed g* (RN) Fixed g* (BN) Random g* (RN) 80 60 60 60 60 40 40 40 40 20 20 Frequency Frequency Frequency Frequency 20 20 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Random g* (BN) Lagrange Permute Y Permute X 80 80 60 60 60 60 40 40 40 40 Frequency Frequency Frequency Frequency 20 20 20 20 0 0 0 0
0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8 0.0 0.4 0.8
p value p value p value p value
Permute T Permute Y (in T) 80 60 60 40 40 20 Frequency Frequency 20 0 0
0.0 0.4 0.8 0.0 0.4 0.8
p value p value
P ˆ2 (b) θj Figure 4.5: Histograms of p-values for simple linear scenario 4 (β = 0.25, γ = 0.5, θ = 0) 78
^ ^ Q Q
RS 0.6 RS ^ ^ QSND QSND
0.8 ^ ^ Qg^ Qg^ 0.5 0.6 0.4 0.3 0.4 0.2 0.2 0.1 0.0 0.0
Fixed g* Fixed g* Lagrange Permute YPermute XPermute T Lagrange Permute YPermute XPermute T Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T) Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T)
(a) Scenario 1 (g(x) = 15I(x1 > 0, x2 > 0)) (b) Scenario 2 (g(x) = 5) 0.25 ^ ^ Q Q
0.6 RS RS ^ ^ QSND QSND ^ ^ Qg^ Qg^ 0.20 0.5 0.4 0.15 0.3 0.10 0.2 0.05 0.1 0.0 0.00
Fixed g* Fixed g* Lagrange Permute YPermute XPermute T Lagrange Permute YPermute XPermute T Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T) Fixed g* (RN)Fixed g* (BN)Rand. g* (RN)Rand. g* (BN) Perm. Y (in T)
(c) Scenario 3 (g(xi) = 5 + ei) (d) Scenario 4 (g(x) = 0) Figure 4.6: Rejection rates (α = 0.05) for complex model simulations 79
Fixed g* Fixed g* (RN) Fixed g* (BN) Fixed g* Fixed g* (RN) Fixed g* (BN) 140 100 60 60 60 60 40 40 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8
P−value P−value P−value P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange Random g* (RN) Random g* (BN) Lagrange 140 120 140 140 60 60 60 60 60 60 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8
P−value P−value P−value P−value P−value P−value
Permute Y Permute X Permute T Permute Y Permute X Permute T 30 30 100 20 20 15 60 15 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value P−value P−value P−value
Permute Y (in T) Permute Y (in T) 100 60 0 0
0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8
P−value P−value
(a) Qˆ(Aˆ)RS (b) Qˆ(Aˆ)SND
Fixed g* Fixed g* (RN) Fixed g* (BN) 100 100 100 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6
P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange 100 100 100 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6
P−value P−value P−value
Permute Y Permute X Permute T 30 120 20 60 15 0 0 0
0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Permute Y (in T) 60 0
0.0 0.2 0.4 0.6 0.8
P−value
(c) Qˆ(Aˆ)gˆ
Figure 4.7: Histograms of p-values for complex scenario 1 (g(x) = 15I(x1 > 0, x2 > 0)) 80
Fixed g* Fixed g* (RN) Fixed g* (BN) Fixed g* Fixed g* (RN) Fixed g* (BN) 30 50 30 50 30 30 15 15 15 20 20 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6
P−value P−value P−value P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange Random g* (RN) Random g* (BN) Lagrange 50 40 30 30 30 30 20 15 20 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8
P−value P−value P−value P−value P−value P−value
Permute Y Permute X Permute T Permute Y Permute X Permute T 40 40 80 80 20 20 40 40 40 40 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value P−value P−value P−value
Permute Y (in T) Permute Y (in T) 40 20 20 0 0
0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8
P−value P−value
(a) Qˆ(Aˆ)RS (b) Qˆ(Aˆ)SND
Fixed g* Fixed g* (RN) Fixed g* (BN) 30 30 30 15 15 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange 40 35 40 20 20 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Permute Y Permute X Permute T 60 100 100 30 0 0 0
0.65 0.75 0.85 0.95 0.0 0.2 0.4 0.6 0.8 1.0 0.5 0.6 0.7 0.8 0.9 1.0
P−value P−value P−value
Permute Y (in T) 60 30 0
0.0 0.2 0.4 0.6 0.8 1.0
P−value
(c) Qˆ(Aˆ)gˆ
Figure 4.8: Histograms of p-values for complex scenario 2 (g(xi) = 5) 81
Fixed g* Fixed g* (RN) Fixed g* (BN) Fixed g* Fixed g* (RN) Fixed g* (BN) 50 25 40 15 15 15 20 20 10 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6
P−value P−value P−value P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange Random g* (RN) Random g* (BN) Lagrange 50 40 40 40 15 15 20 20 20 20 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.0 0.2 0.4 0.6 0.8
P−value P−value P−value P−value P−value P−value
Permute Y Permute X Permute T Permute Y Permute X Permute T 100 80 40 80 20 40 20 40 40 40 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value P−value P−value P−value
Permute Y (in T) Permute Y (in T) 40 40 20 20 0 0
0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8
P−value P−value
(a) Qˆ(Aˆ)RS (b) Qˆ(Aˆ)SND
Fixed g* Fixed g* (RN) Fixed g* (BN) 30 30 30 15 15 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange 30 30 15 15 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Permute Y Permute X Permute T 50 100 100 20 0 0 0
0.6 0.7 0.8 0.9 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.5 0.6 0.7 0.8 0.9 1.0
P−value P−value P−value
Permute Y (in T) 50 20 0
0.0 0.2 0.4 0.6 0.8 1.0
P−value
(c) Qˆ(Aˆ)gˆ
Figure 4.9: Histograms of p-values for complex scenario 3 (g(xi) = 5 + ei) 82
Fixed g* Fixed g* (RN) Fixed g* (BN) Fixed g* Fixed g* (RN) Fixed g* (BN) 40 40 40 40 40 20 20 20 20 20 20 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange Random g* (RN) Random g* (BN) Lagrange 40 40 40 40 30 30 20 20 20 20 15 15 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value P−value P−value P−value
Permute Y Permute X Permute T Permute Y Permute X Permute T 35 40 20 20 20 20 15 20 0 0 0 0 0 0
0.0 0.2 0.4 0.6 0.8 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value P−value P−value P−value
Permute Y (in T) Permute Y (in T) 50 40 20 20 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value
(a) Qˆ(Aˆ)RS (b) Qˆ(Aˆ)SND
Fixed g* Fixed g* (RN) Fixed g* (BN) 30 30 30 15 15 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Random g* (RN) Random g* (BN) Lagrange 30 30 20 15 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Permute Y Permute X Permute T 30 15 20 15 0 0 0
0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0
P−value P−value P−value
Permute Y (in T) 20 0
0.0 0.2 0.4 0.6 0.8 1.0
P−value
(c) Qˆ(Aˆ)gˆ Figure 4.10: Histograms of p-values for complex scenario 3 (g(x) = 0) CHAPTER 5
Discussion and future work
We proposed two methods which use randomized clinical trial data to identify
subgroups of enhanced treatment effect. The first method was a penalized monotone
single-index model, and could be used for subgroup identification in a variety of
ways. For instance, one could consider using this model for the variable selection
stage of an existing subgroup identification procedure, such as Virtual Twins [Foster
et al., 2011]. That is, this model could be used as a replacement for the single
regression tree in the second stage of the Virtual Twins procedure. One could also
consider using a penalized monotone single-index model to estimate the treatment
effect directly in the Average Value procedure, converting it to a one-stage procedure,
and eliminating the need for the computationally expensive subgroup search. By
penalizing the index parameter in this model, we are able to greatly reduce model
complexity, which, combined with the monotonicity constraint on the function η, means the resulting subgroup will generally be relatively easy to understand. The second method is the Average Value procedure mentioned above, which can be viewed as a model-based alternative to the Virtual Twins procedure, and which was found to very effectively identify truly important covariates in our simulation study. Though
83 84 this procedure is more computationally demanding than Virtual Twins, and was in some ways outperformed by Virtual Twins in our simulations, it has the advantage of identifying a single, contiguous region, which will often depend on fewer covariates than the subgroup identified by Virtual Twins, and may thus be somewhat easier to understand.
In addition to the subgroup identification procedures, we proposed a number of permutation-based methods for obtaining p-values for treatment-by-covariate inter- actions, and showed that they perform well compared to simple permutation tests, especially for more complex models and somewhat ad hoc test statistics. We also considered the use of these methods to obtain p-values for the enhancement metric discussed by Foster et al. [2011]. Having p-values along with enhancement metric estimates could help to further reduce the chances of falsely declaring an identified subgroup to be enhanced.
Overall, we feel the methods proposed in this dissertation represent a meaning- ful contribution to the field of subgroup analysis. We showed that, in many cases, very simple subgroups can accurately identify subjects who will show an enhanced response to treatment. Additionally, we considered a number of methods for evalu- ating the identified regions, such as permutation-based p-values for interaction tests.
We believe such post-identification evaluation is important, as most subgroup identi-
fication procedures will nearly always identify a region, regardless of whether or not it is truly enhanced. Using the proposed methods, it may be possible to make more informed (and more confident) treatment decisions in the future using only a very limited amount of patient information. This lack of necessary information, along with the simple form (and resulting easy interpretability) of the subgroups identified by our methods, should lead to treatment assignment rules which will see a good deal of 85 real-world use. Because of this, we believe the proposed methods may also encourage others working in the field of subgroup analysis to consider giving more weight to interpretability.
There are a variety of possible extensions to the methods considered in this dis- sertation. To further reduce the risk of false positives, we could consider the use of external information to define a subgroup. This could be done by developing an approach for weighting covariates which were pre-determined to be important, so that some are more likely than others to be chosen to define the “enhanced” region.
Alternatively, we could consider the development of a method for pre-screening the covariates. Such a method could be used, say, after the first step of the Virtual
Twins or Average Value procedures, so that only a subset of the covariates would be included as candidates for defining potential subgroups. This could be particularly helpful if we wish to consider other forms of data, such as genetic data, which could have thousands of covariates.
Thus far, we have considered the case where only two treatment options exist, but in many cases there may be several potentially good treatment options. Therefore, it would be useful to modify the proposed methods so that multiple treatment options could be considered. One simple way to do this would be to consider a different anal- ysis for each unique treatment comparison, so that we would have several treatment effect estimates instead of one; however, this could dramatically increase the potential for false positive findings, and the results of such an analysis could be difficult to in- terpret. In some cases, one may know a priori which specific treatment comparisons are of interest, and could thus potentially reduce the number of unique treatment comparisons considered, thereby potentially reducing the risk for false findings and allowing for more interpretable results. For situations where one doesn’t know which 86 specific comparisons are of interest, it may also be interesting to consider the devel- opment of some sort of screening method which “weeds out” comparisons between similar treatments.
Another issue is the implementation of subroup identification procedures when there is missing data in the outcome, covariates or both. In such situations, multiple imputation is often employed, but combining inferences from multiple imputed data sets could be difficult when the output of a method is a subregion of the covariate space, rather than a numeric value, such as a parameter estimate or test statistic. One option would be to implement multiple imputation in the treatment effect estimation stage, but then use the observed data (with missingness) in the subgroup identification stage, but this is clearly not ideal. Thus, it would be very interesting to consider the development of a method for combining inferences from multiple imputed data sets when the object of interest is a subregion of the design space.
To this point, we have focused on using baseline information from RCT data to predict a patient’s response to treatment, but have not suggested how post-treatment information may be used. It would be very interesting to work on developing methods which use post-treatment information, in addition to baseline information, to better assign treatment to patients. This could be done within the framework of dynamic treatment regimes, in which treatment decisions at a given time are made using a patient’s history up to that time. A number of authors, including Murphy [2002],
Lavori and Dawson [2004], Robins [2004], Laan and Petersen [2004], Murphy [2005],
Laber et al. [2010], and Shortreed et al. [2011] have considered dynamic treatment regimes. Though very nice to work with, RCT data is often quite difficult to obtain, so the extension of the proposed methods to data from observational studies is also of interest. 87
APPENDIX Appendix A
Asymptotics for Chapter 1
Statement of theorem
We establish the oracle properties for unconstrained adaptive lasso penalized
single-index model estimates. Consider the following setup and regularity conditions
of Hardle et al. [1993]. Assume the data {(xi, yi):, i = 1, . . . , n} come from (2.1), where β0 is the true value of the index parameter, and the last q < p elements of β0
∗ ˆ p are 0. Let A = {j : β0,j 6= 0} and An = {j : βj 6= 0}. Let H ⊆ R be a set chosen so denominators in formulas for kernel estimators are not too close to 0, where H is the W 0(11) W 0(21) union of a finite number of convex sets. Define W 0 = to be the W 0(12) W 0(22) p × p matrix:
Z T T T T T 0 T 2 x − E(XH |β0 XH = β0 x) x − E(XH |β0 XH = β0 x) × η (β0 x) f(x)dx, H
where X is a random variable with the design density f, W 0(11) is (p−q)×(p−q) and
δ XH has the distribution of X, conditional on X ∈ H. Given δ > 0, let H denote the
p T δ set of all points in R distant no further than δ from H. Put U = {β0 x : x ∈ H },
88 89
T and let ζ denote the density of β0 X. We define the following conditions for some
δ > 0:
1. f is bounded away from 0 on Hδ and has two bounded derivatives there;
2. η and ζ have two bounded, continuous derivatives on U ;
3. K is supported on the interval (−1, 1) and is a symmetric probability density,
with a bounded derivative;
2 2 2 4. E(i|xi) = 0, E(i |xi) = σ (xi) for all i, where the function σ is bounded and
m continuous and supiE|i| = Mm < ∞ for all m.
As noted by Hardle et al. [1993], the emphasis on two derivatives in (1) and (2) is
motivated by the use of a second-order kernel, and the restriction in (1) that f be
bounded away from 0 on Hδ ensures with high probability that the denominator in
T (2.3) is bounded away from zero for t = β x, where x ∈ H and β is close to β0. Let
B denote the set of all unit p-vectors. Given C > 0, and 0 < C1 < C2 < ∞, Bn =
−1/2 −1/5 −1/5 {β ∈ B : kβ − β0k ≤ Cn }, and Hn = {h : C1n ≤ h ≤ C2n }. We ˆ √ assume that β ∈ Bn and h ∈ Hn. This is likely to be true if we start with a n-
consistent estimator, such as that shown by Ichimura [1993] to exist for unpenalized,
unconstrained SIM.
Theorem A.1 (Oracle Properties). Let (x1, y1),..., (xn, yn) be iid observations
from model (2.1) such that conditions (1)-(4) hold. Suppose that W 0 is positive-
√λn (γ−1)/2 3 definite, and that n → 0 and λnn → ∞, where γ ∈ (0, 5 ]. Then the adaptive- LASSO penalized single-index model estimates must satisfy:
∗ 1. Consistency in variable selection: limnP (An = A) = 1; 90
√ ˆ 2 −1 2. Asymptotic normality: n × (βA − β0A) →d N(0, σ W 0(11)).
Thus, the adaptive lasso penalized single-index model estimates perform as well as if the true nonzero elements of β0 were known.
Proofs
Theorem 1, part (b)
Let Sˆ(β, h) be the non-penalized sum of squares. Under conditions (i)-(iv), we know from Hardle et al. [1993] that
ˆ ˜ S(β, h) = S(β) + T (h) + R1(β, h) + R2(h),
1/5 ˜ where supβ∈Bn,h∈Hn |R1(β, h)| = op(n ), and S(β) =
1/2 1/2 n{W (β − β ) − √σ Z}T {W (β − β ) − √σ Z} + R (β), where sup |R (β)| = 0 0 n 0 0 n 4 β∈Bn 4
op(1). From this point on, we drop any terms not depending on β, since β is our ˜ primary interest. Also, since R4 is of smaller order than S, it is negligible. Thus, we ˜ ˜ ˜ P can treat S as our objective function. Considering now S2 = S + λn wˆj|βj|, we
√u can apply reasoning similar to Zou [2006]. Let β = β0 + n , where kuk ≤ C and
ˆ −γ wˆj = |βinit| . Then we have:
( )T ( ) p 1 u σ 1 u σ X uj S˜ (u) = n W 2 √ − √ Z W 2 √ − √ Z + λ wˆ β + √ + o (1). 2 0 n n 0 n n n j 0,j n p j=1 91
˜ ˆ √uˆ Where Z →d T ∼ N(0, Ip). Let uˆ = argmin S2(u); then β = β0 + n , or uˆ = √ ˆ ˜ ˜ (n) n × (β − β0) Thus, we know S2(u) − S2(0) = V (u), where
V (n)(u) =
p ! 1 1 1 λn X √ uj uT W 2 W 2 u − 2σuT W 2 Z + √ nwˆ β + √ − |β | + o (1). 0 0 0 n j 0,j n 0,j p j=1
The first term does not depend on n and we know that Z →d T ∼ N(0, Ip). The lim-
iting behavior of the third term can be argued exactly as in Zou [2006]. In particular,
√ u −γ √j if β0,j 6= 0, then we knoww ˆj →p |β0,j| and n(|β0,j + n | − |β0,j|) →p ujsign(β0,j),
√ u √λn √j √λn so by Slutsky’s theorem we know n wˆj n(|β0,j + n | − |β0,j|) →p 0, since n → 0,
√ u √j √λn as long as uj < ∞. If β0,j = 0, then n(|β0,j + n | − |β0,j|) = |uj| and n wˆj = √ √ √λn γ/2 ˆ −γ ˆ n n (| nβinit,j|) , where nβinit,j = Op(1). Therefore, using Slutsky’s theorem
(n) again, we can see that V (u) →d V (u) for every u, where
1 T T 2 uAW 0(11)uA − 2σuAW T A if uj = 0 ∀j∈ / A V (u) = 0(11) ∞ otherwise.
(n) Note that choosing uj to be finite for β0,j 6= 0 gives finite values of V , whereas
(n) if uj is not finite for β0,j 6= 0, V is infinite, so the optimal u must be finite. We
(n) know that V is convex (if W 0 is positive-definite), and the unique minimum of V
1 − 2 is (σW 0(11)T A, 0). Thus, following the epi-convergence argument used by Zou [2006], we have
1 − 2 uˆ A →d σW 0(11)T A and uˆ Ac →d 0.
√ ˆ 2 −1 Since T A ∼ N(0, I), we know n×(βA −β0A) →d N(0, σ W 0(11)), and we are done. 92
Theorem 1, part (a)
Again we can follow the general framework of Zou [2006]. We know that ∀j ∈ A, ˆ the asymptotic normality results above indicate that βj →p β0,j; thus meaning that
∗ 0 0 ∗ P (j ∈ An) → 1. Therefore, we need only show that ∀j ∈/ A,P (j ∈ An) → 0.
1 0 ∗ 2 ˆ Suppose that j ∈ An. By the KKT optimality conditions, we know that 2n{W 0 (β−
1 1 1 1 − T 2 ˆ ˆ 2 T 2 ˆ β0) − n 2 σZ} W 0 = λn(w ˆ1sign(β1), ··· , wˆpsign(βp)), so 2n[W 0 ]j0 {W 0 (β − β0) −
− 1 ˆ n 2 σZ} = λnwˆj0 sign(βj0 ). We know generally that |sign(t)| → 1 as t → 0, and √ λn λn γ/2 −γ √ 0 √ ˆ 0 n wˆj = n n (| nβinit,j |) →p ∞. However,
1 1 1 1 1 √ 1 2 2 T 2 − 2 T 2 2 T √ n[W ] 0 {W (βˆ − β ) − n 2 σZ} = 2[W ] 0 W n(βˆ − β ) − 2σ[W ] 0 Z, n 0 j 0 0 0 j 0 0 0 j
where both terms on the right hand side converge in distribution to normals. Thus,
we know
1 1 1 0 ∗ 2 T 2 ˆ − 2 ˆ P (j ∈ An) ≤ P 2n[W 0 ]j0 {W 0 (β − β0) − n σZ} = λnwˆj0 sign(βj0 ) → 0,
and we are done. BIBLIOGRAPHY
93 94
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